Safety and Effects of Brimonidine Intravitreal Implant in Patients With Glaucomatous Optic Neuropathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Effects of Brimonidine Intravitreal Implant in Patients With Glaucomatous Optic Neuropathy (NCT00693485), a randomized phase 2 study. The primary outcome is Percentage of Patients With a Visual Field Improvement in the Study Eye.

2. Clinical Question

This question concerns a measured change in visual function, rather than a direct measure of pressure in the eye or a patient-reported outcome. The registry also lists change from baseline in Best Corrected Visual Acuity (BCVA) in the study eye as a secondary outcome. The posted record does not report its results in the material. The primary comparison is therefore the percentage with visual-field improvement in each randomized arm, interpreted alongside the uncertainty in the posted estimates.

3. Trial Design

The registry describes a randomized, triple-masked, parallel-group phase 2 trial with a sham control. The brief summary characterizes the study as multicenter and patient-masked; the registry record does not specify which other roles were masked. The interventions were the 400 ug implant, the 200 ug implant, and sham treatment without an implant. Each was administered to the study eye at Day 1 according to the arm descriptions.

The registry lists enrollment as 70. The posted primary endpoint summaries report 25 patients in the 400 ug implant arm, 21 in the 200 ug implant arm, and 24 in the sham arm. The endpoint population is the Safety Population, defined in the record as all patients who received 1 dose of study medication or sham treatment. These arm counts should be understood in the context of that stated population and endpoint, rather than assumed to describe every possible analysis population.

The listed study dates are 2008-09 for the start and 2011-01 for primary completion. The study status is completed. The brief summary says patients would be followed for up to 1 year, while the primary endpoint timeframe is Baseline and Month 6. The registry record does not report the original sample-size justification, the reasons for the enrollment figure, or the trial's original statistical analysis plan. Randomization and masking describe design features, but do not by themselves determine how endpoint data were analyzed. No analysis results are listed in the registry's analyses count.

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

Analysis population for the primary outcome, as defined in the registry: Safety Population: all patients who received 1 dose of study medication or sham treatment

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 With a Visual Field Improvement in the Study Eye, measured over Baseline, Month 6.

The primary endpoint is the percentage of patients with a visual-field improvement in the study eye. The assessment uses the Humphrey Field Analyzer (HFA 24-2) full threshold test and clinical expertise. The record describes improvement as an increase in the field of vision and gives Baseline and Month 6 as the timeframe. The outcome is therefore a binary classification at the patient level: a patient is counted as having improvement or not having improvement under the stated assessment.

Reporting a percentage makes the endpoint interpretable as the share of the analyzed group meeting the improvement criterion. It does not convey the size of any individual patient's change, and it does not show how the visual field changed in people who were not classified as improved. The registry does not report the specific clinical decision rules used alongside the test, nor does it provide further details on how borderline or unmeasurable results were handled.

This endpoint is used to address the trial's stated interest in visual function. It differs from Best Corrected Visual Acuity, which is listed as a secondary outcome, and from safety outcomes. The primary endpoint summaries are presented for the Safety Population. Interpretation should therefore remain tied to the stated visual-field definition, study eye, timepoint, and population, rather than generalized to other aspects of vision or to longer-term outcomes that are not reported for this endpoint.

7. Results Posted in the Registry

• 400 ug Brimonidine Implant: 12.0% (3/25) versus 4.2% (1/24) on control; risk difference 7.8 percentage points (95% CI -7.2 to 22.9), risk ratio 2.88 (0.32–25.80); unadjusted two-proportion z-test p = 0.317.
• 200 ug Brimonidine Implant: 9.5% (2/21) versus 4.2% (1/24) on control; risk difference 5.4 percentage points (95% CI -9.5 to 20.2), risk ratio 2.29 (0.22–23.44); unadjusted two-proportion z-test p = 0.472.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a risk difference describe?

For a binary outcome such as whether a patient had visual-field improvement, a risk difference describes the difference between the proportions meeting the endpoint in two groups. A value of zero corresponds to equal proportions. A positive value indicates a higher observed proportion in the implant group than in sham; a negative value indicates a lower observed proportion. This measure keeps the comparison on the percentage-point scale and can be read alongside each arm's event percentage.

The posted comparisons are implant versus sham, separately for the 400 ug and 200 ug implants. The registry reports the arm percentages and unadjusted risk-difference estimates with confidence intervals. The confidence interval represents uncertainty in the estimated difference under the calculation method; it is not a range containing a known, fixed treatment effect with certainty. Because the intervals span values on either side of zero, the comparisons do not rule out no difference or a difference in either direction.

What do the p-values say?

The reported comparison p-values are unadjusted recalculations from the posted summary statistics. They assess how compatible the observed data are with a no-difference hypothesis under the assumptions of the calculation. The p-values are 0.317 for the 400 ug implant comparison and 0.472 for the 200 ug implant comparison. They are not probabilities that the null hypothesis is true, and they do not quantify the probability that the results will replicate. A p-value also does not reveal whether an effect, if present, would be important in practice.

“Unadjusted” matters because these comparisons are not reported as adjusted for multiple testing. If many endpoints or comparisons are examined, the chance of encountering a small p-value by chance can increase. The registry record does not report a multiplicity strategy or a prespecified hierarchy for interpreting outcomes. The primary endpoint is identified, but that alone does not establish how the trial's original analysis handled multiple comparisons.

Why use confidence intervals as well as p-values?

A confidence interval communicates the range of effect estimates compatible with the data under the method used. Its width reflects precision: a wider interval indicates greater uncertainty. Intervals are helpful because they show not just whether the data are inconsistent with zero at a chosen threshold, but also which effect sizes remain plausible. In this trial, the arm counts are limited and the endpoint is uncommon in the posted summaries, so uncertainty is an important part of interpretation. The interval does not guarantee that the true effect lies within it, and it does not account for unreported sources of bias or analysis choices.

What does “binary percentage” mean?

The endpoint classifies patients according to whether they had an improvement. A percentage is the proportion of the endpoint population with that classification. This representation differs from a continuous change score, which would describe the amount of change in a measurement, and from a time-to-event outcome, which incorporates when an event occurs. Here, the reported endpoint does not show the degree of visual-field improvement among those classified as improved. It also does not describe the full distribution of visual-field measurements.

Binary outcomes can be sensitive to how an improvement threshold or clinical classification is defined. The registry says the determination used the HFA 24-2 full threshold test and clinical expertise, but the detailed classification rules are not reported in the registry record. That limits independent assessment of how the endpoint classification was applied.

Why can small event counts produce uncertainty?

When relatively few patients meet an endpoint, changing the classification of a small number of observations can materially alter a group percentage. Estimates of differences are consequently sensitive to the observed event counts, and confidence intervals can be wide. This is a general statistical property of binary outcomes with sparse events, not evidence by itself of a flaw in the trial. It helps explain why descriptive separation between percentages can coexist with considerable uncertainty about the comparative effect.

The record also presents relative measures, including risk ratios and odds ratios, but the interpretation emphasizes the risk difference because it directly contrasts the percentages on an absolute scale. Relative measures answer a different question and can look large when the event is uncommon, while still being imprecise. They should not be interpreted without their uncertainty intervals or the underlying event proportions.

What is not specified about the analysis?

The registry record does not report the original analysis plan, covariate adjustment, handling of missing endpoint observations, or any interim analysis. The record identifies a Safety Population for the primary endpoint, but does not describe other analysis populations or explain whether all randomized patients contributed to the endpoint summary. It also does not report a sponsor analysis result for these comparisons. Without those details, the posted summaries support descriptive interpretation and the stated unadjusted recalculations, but not reconstruction of the trial's complete analysis process.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the comparison. The posted confidence intervals for both risk differences are wide and extend across zero. That means the observed data do not pin down a single direction or a narrow range of possible differences. The intervals include values consistent with a lower improvement proportion in an implant group, no difference, and a higher proportion. This is why the percentages alone should not be read as conclusive evidence of a comparative effect.

The uncertainty is consistent with the limited number of patients in each endpoint arm and the small numbers classified as improved. In general, estimates from sparse binary outcomes tend to be imprecise because a small change in event counts can affect the estimated proportion. This is a general statistical explanation; it does not identify why any individual patient was or was not classified as improved.

A confidence interval is not a probability distribution for the true effect, and its endpoints are not guaranteed bounds on that effect. It describes uncertainty under the method used and the assumptions underlying the calculation. It does not include uncertainty from unreported choices such as missing-data handling, endpoint classification details, or multiplicity adjustment. The registry record does not report those analysis details.

The unadjusted p-values are consistent with the broad uncertainty: 0.317 for the 400 ug comparison and 0.472 for the 200 ug comparison. Neither comparison provides strong evidence against a no-difference hypothesis, but neither establishes that effects are absent. The intervals are therefore important for distinguishing lack of a clear statistical signal from proof of no effect. The posted results leave substantial uncertainty about the size and direction of the comparative differences.

11. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effects in the posted comparisons; they are not the trial's original design calculations. These figures are participants per arm, not total event counts. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The original trial's sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned participants per arm for a design with an 80% chance of detecting the specified effect under the calculation assumptions, if that effect is the true one. The 90% power column gives the corresponding per-arm planning figure for a design with a 90% chance. These are design probabilities under assumptions, not guarantees for a future study. They do not describe the probability that the trial result is correct.

For the 400 ug comparison, planning for 100% of the observed effect gives 189 participants per arm for 80% power and 253 participants per arm for 90% power. Planning for 75% of the observed effect gives 299 participants per arm for 80% power and 400 participants per arm for 90% power. Planning for 50% of the observed effect gives 588 participants per arm for 80% power and 786 participants per arm for 90% power.

For the 200 ug comparison, planning for 100% of the observed effect gives 348 participants per arm for 80% power and 465 participants per arm for 90% power. Planning for 75% of the observed effect gives 563 participants per arm for 80% power and 753 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,138 participants per arm for 80% power and 1,522 participants per arm for 90% power. Smaller effects need more participants to detect under the same assumptions. These figures are not observed power.

12. 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 = 0.042; treatment proportion p₁ = 0.120; average p̄ = 0.081.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3855 = 0.7555.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3815 = 0.3211.
4. n = (0.7555 + 0.3211)² / (0.0783)² = 188.9, rounded up to 189 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 <- 0.0416666666666667                          # control proportion
p1 <- 0.12                          # 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(693485)
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 = 189 (80% power), 253 (90% power)
 75% of observed effect: n per arm = 299 (80% power), 400 (90% power)
 50% of observed effect: n per arm = 588 (80% power), 786 (90% power)
power.prop.test: 188.9 
Simulated power at n = 189 per arm: 0.818 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record identifies visual-field improvement as the primary endpoint and lists change from baseline in BCVA in the study eye as a secondary outcome. It does not report a multiplicity adjustment, a testing hierarchy, or the planned approach to interpreting more than one endpoint or comparison. The unadjusted p-values should therefore be read as nominal comparisons rather than as results shown to control the overall chance of a false-positive finding across all possible tests.

The record does not report how missing primary endpoint observations were handled, whether any imputation was used, or whether patients without an evaluable Month 6 assessment were included in another way. It does not report a detailed accounting of patients excluded from the endpoint summaries or reasons for missing data. The stated Safety Population consists of patients who received 1 dose of study medication or sham treatment; the registry does not provide further analysis-population definitions for this endpoint.

Randomization is listed as a design feature, but the posted record does not say whether the primary comparison was adjusted for baseline factors or whether the analysis followed a particular intention-to-treat definition. The masking classification is triple, while the brief summary specifically describes patient masking. Details about masking of other roles are not reported in the registry record. The registry analyses count is 0, so a complete trial analysis plan and sponsor-reported inferential results are not available in the posted information.

These gaps do not change the descriptive percentages, but they limit what can be concluded about the exact analysis population, the impact of missing observations, and the interpretation of nominal tests across outcomes. The results are best treated as the posted endpoint summaries and unadjusted recalculations, with those analysis details remaining unresolved.

14. 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: arteriospasm coronary (4.8%), cataract (4.8%), concussion (4.8%), arthritis (4.8%), squamous cell carcinoma (4.8%).

The registry reports serious adverse events and other adverse events by arm. For serious adverse events, 3 patients in the 400 ug implant group, 5 in the 200 ug implant group, and 1 in the sham group were affected. For other adverse events, the corresponding affected counts were 18, 19, and 20. The counts are reported against at-risk group sizes of 25, 21, and 24, respectively. These are descriptive safety summaries, not randomized efficacy comparisons.

The serious-event terms listed with percentages include Arteriospasm coronary, Cataract, Concussion, Arthritis, and Squamous cell carcinoma, each at 4.8%, and Osteoarthritis at 4.2%. The registry record does not provide enough detail in these summaries to infer causality from a listed term or to determine whether a particular event was related to treatment. Death counts are not reported in the registry record.

Safety counts should be read with their denominators and the trial's limited size in mind. A count does not indicate severity beyond the serious-event classification, duration, recurrence, or individual clinical course. The posted summaries do not establish comparative safety, and they do not replace examination of event descriptions and the full safety analysis.

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

The results establish what was observed for the posted primary endpoint summaries: the percentages classified as having visual-field improvement were 12.0% for the 400 ug implant, 9.5% for the 200 ug implant, and 4.2% for sham. The recalculated unadjusted comparisons have p-values of 0.317 and 0.472. The confidence intervals span both sides of no difference, indicating substantial uncertainty about the comparative effects.

These findings do not establish that either implant is superior to sham, and they do not establish that the groups are equivalent. A comparison that does not provide strong statistical evidence against no difference is not proof that there is no effect. Likewise, a higher observed percentage in an implant group does not by itself show that the difference is reliable or clinically important. The record does not report a threshold for a clinically meaningful change in the primary endpoint.

The endpoint captures whether visual-field improvement was classified at the stated timeframe, not the magnitude of change, every aspect of visual function, or long-term outcome. The registry lists BCVA as a secondary outcome but does not report its result in the posted information. The results also do not determine the benefit-risk balance, because a complete interpretation would require fuller efficacy and safety evidence than these summaries provide.

The trial was a phase 2, randomized, sham-controlled study, but its posted arm sizes and uncertainty limit precision. The registry record does not report the original statistical plan, missing-data methods, multiplicity handling, or the original sample-size justification. The findings should therefore be interpreted as descriptive evidence from this trial, with uncertainty, rather than as a definitive answer about effectiveness or safety in a broader population.

16. Why This Trial Matters Statistically

This trial illustrates an important distinction in clinical statistics: an apparent separation in observed percentages is not the same as precise evidence of a difference. The visual-field improvement percentages are higher in the implant groups than in sham, but the risk-difference intervals extend across zero and the unadjusted p-values are not small. Reading the estimates and their uncertainty together avoids treating a descriptive pattern as a conclusive result.

The endpoint is binary, so the analysis reduces a visual-field assessment to whether each patient was classified as improved. That can make a result easier to summarize, but it does not show the degree of change or the experience of patients who did not meet the classification. The record describes use of the HFA 24-2 test and clinical expertise, while leaving the detailed classification rules unreported. This makes endpoint definition and transparent reporting particularly relevant to interpretation.

The trial also highlights the planning implications of uncertain, sparse outcomes. The sample-size illustrations indicate that planning to detect a smaller fraction of the observed effect requires more participants per arm under the stated assumptions. These calculations are not the original design rationale, which is not reported, and should be understood as prospective planning illustrations rather than evidence about the trial's power.

Finally, the registry record leaves important analysis details unreported, including missing-data methods, multiplicity handling, and a sponsor analysis for the primary comparisons. Recognizing those limits is part of statistical interpretation: the posted data support a careful description of what was observed, but do not answer every question a full trial report might address.

17. 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 posted primary endpoint summaries are based on relatively small arm counts, and only a small number of patients in each group were classified as having improvement. The resulting comparisons are imprecise, as reflected by intervals that extend across no difference. These data cannot finely distinguish among plausible comparative effects.

The endpoint combines a Humphrey Field Analyzer assessment with clinical expertise, but the detailed criteria used to classify improvement are not reported in the registry record. The record also does not explain handling of missing Month 6 assessments, withdrawals, or unevaluable tests. The primary endpoint population is defined as the Safety Population, but further detail about endpoint-specific analysis inclusion is not reported.

The original statistical analysis plan, multiplicity approach, baseline adjustment, and interim analysis information are not reported in the registry record. The posted comparison p-values are unadjusted recalculations, and the registry analyses count is 0. Therefore, the available information does not support reconstruction of the sponsor's full analysis or confirmation of all prespecified analysis choices.

The primary endpoint addresses visual-field improvement at Month 6. It does not provide a measure of the magnitude of improvement or establish longer-term outcomes. Although BCVA is listed as a secondary outcome, its result is not reported in the posted information. The safety summaries are also limited: death counts are not reported, and the brief event listings do not give enough information to establish causality or describe individual event courses.

The registry record describes the study as multicenter and randomized, but does not provide further detail on sites or generalizability. The original sample-size justification is not reported, and the planning illustrations are not the trial's own design calculations. These limitations warrant cautious interpretation without negating the descriptive information that is posted.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Effects of Brimonidine Intravitreal Implant in Patients With Glaucomatous Optic Neuropathy — NCT00693485.
• Registry record last updated 2013-04-24; status last verified 2013-03.
• Results first posted 2013-04-24.
• 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.

21. Record Summary

NCT00693485 is a completed, randomized, triple-masked, parallel-group phase 2 trial sponsored by Allergan. It studied 400 ug and 200 ug brimonidine intravitreal implants against sham in patients with glaucomatous optic neuropathy. The registry lists open-angle glaucoma as a condition and describes the study as multicenter.

The primary endpoint was the percentage of patients with visual-field improvement in the study eye at Baseline and Month 6, assessed using the HFA 24-2 full threshold test and clinical expertise. Posted percentages were 12.0% for the 400 ug implant, 9.5% for the 200 ug implant, and 4.2% for sham. The unadjusted recalculated comparisons are uncertain, with p-values of 0.317 and 0.472 and confidence intervals spanning zero.

The record lists change from baseline in BCVA as a secondary outcome, but its result is not reported in the posted information. The registry record does not report the original sample-size justification, missing-data methods, multiplicity strategy, or sponsor analysis results for these comparisons.