A Study of the Safety and Efficacy of a New Treatment for Non-Infectious Intermediate or Posterior Uveitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Safety and Efficacy of a New Treatment for Non-Infectious Intermediate or Posterior Uveitis (NCT00333814), a randomized phase 2, phase 3 study. The primary outcome is Percentage of Patients With Vitreous Haze (Ocular Inflammation) Score of Zero.

2. Clinical Question

The endpoint is a binary outcome: each patient either had a score of zero at the assessment or did not. The principal statistical contrast is therefore the difference in the proportion meeting that endpoint between each dexamethasone group and the sham group. The registry reports the outcome percentages by arm and unadjusted comparisons, including risk differences and confidence intervals.

This question concerns a specified ocular inflammation measure at a particular follow-up time. It does not, by itself, describe other aspects of disease, longer-term outcomes, or the overall balance of benefits and harms. The registry record does not report a posted analysis of secondary outcomes.

3. Trial Design

The registry identifies this as a Phase 2 and Phase 3 study with randomized allocation and a parallel-group model. It was quadruple-masked. The posted arms were dexamethasone 350 µg, dexamethasone 700 µg, and sham injection. The registry reports enrollment of 229. The sponsor was Allergan.

The listed start was 2006-05, and primary completion was 2008-12. The study status is completed. Its brief description says it evaluated the safety and efficacy of an intravitreal dexamethasone implant for non-infectious intermediate or posterior uveitis. Those descriptions establish the broad clinical and design context, but they do not provide details such as the exact masking procedures or how randomization was implemented; those details are not reported in the registry record.

The primary outcome was the percentage of patients with a vitreous haze score of zero at Week 8. Its stated analysis population was intent to treat. Arm-level results were 35.5% for dexamethasone 350 µg, 46.8% for dexamethasone 700 µg, and 11.8% for sham. The posted comparisons use 76 patients in the sham group and 76 or 77 patients in the respective dexamethasone groups.

A randomized comparison is designed to assess differences between assigned groups while reducing the influence of systematic differences in treatment assignment. Masking can reduce some forms of influence on care or outcome assessment, but the registry record does not describe which people were masked or the procedures used. It also does not report the original sample-size justification, the trial’s full statistical analysis plan, or whether interim analyses were planned or conducted.

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: Intent to Treat

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 Vitreous Haze (Ocular Inflammation) Score of Zero, measured over Week 8.

The primary endpoint is the percentage of patients with a vitreous haze score of zero at Week 8. Vitreous haze is an ocular inflammation measure. The registry describes a standardized scale from 0 to +4: 0 means no inflammation, while +4 means the optic nerve head is not visible because of severe haze. The endpoint reduces the scale to whether a patient reached the zero-score category at the specified assessment.

This is a binary outcome, so the reported percentage represents the fraction of patients in an arm who met the endpoint. It offers a direct way to compare the frequency of a prespecified clinical state across randomized groups. A zero score is a clear threshold, but a percentage meeting that threshold does not show the full distribution of scores among patients who did not reach zero. Nor does the measure alone describe other clinical outcomes, changes over time, or safety.

The endpoint is stated for the intent-to-treat population. The registry record does not explain how missing Week 8 measurements were handled or whether any other rules were used to determine inclusion in the endpoint analysis. These details matter when interpreting percentages, because the handling of unavailable assessments can affect which observations contribute to an estimate.

7. Results Posted in the Registry

• Dexamethasone 350 µg: 35.5% (27/76) versus 11.8% (9/76) on control; risk difference 23.7 percentage points (95% CI 10.7 to 36.7), risk ratio 3.00 (1.51–5.95); unadjusted two-proportion z-test p = <0.001.
• Dexamethasone 700 µg: 46.8% (36/77) versus 11.8% (9/76) on control; risk difference 34.9 percentage points (95% CI 21.6 to 48.2), risk ratio 3.95 (2.04–7.62); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary measure is binary: patients are classified according to whether the Week 8 vitreous haze score was zero. For a binary outcome, the basic arm-level summary is the proportion meeting the endpoint. The posted percentages are 35.5% for dexamethasone 350 µg, 46.8% for dexamethasone 700 µg, and 11.8% for sham. These proportions preserve the meaning of the clinical threshold, but they do not retain information about which nonzero scores occurred.

A risk difference subtracts the comparison-group proportion from the intervention-group proportion. In the posted comparisons, the risk differences are 0.237 for 350 µg versus sham and 0.349 for 700 µg versus sham. Risk difference is an absolute contrast on the probability scale. It is useful for understanding how far apart the observed proportions are, while still depending on the underlying event frequency in each group.

A risk ratio compares the intervention-group probability with the comparison-group probability by division. The registry reports 3.0 for 350 µg versus sham and 3.948 for 700 µg versus sham. An odds ratio compares the odds of meeting the endpoint between groups, where odds are formed from the probability of meeting the endpoint relative to the probability of not meeting it. The posted odds ratios are 4.102 and 6.537, respectively. Ratios are relative measures, whereas the risk difference is an absolute measure. Their numerical sizes cannot be directly compared as though they used the same scale.

Confidence intervals provide a range of values compatible with the estimate under the statistical model and its assumptions. They convey uncertainty as well as the estimated direction and magnitude. A wide interval indicates less precision than a narrow interval. A confidence interval is not a guarantee that the true value lies inside its particular limits, and its interpretation depends on the method used to construct it. The registry record does not describe the confidence-interval method for the trial’s own analysis.

The posted p-values are unadjusted: <0.001 for each comparison with sham. In general, a p-value describes how unusual data at least as incompatible with a null hypothesis would be under that null hypothesis and the model assumptions. It is not a measure of effect size, does not indicate whether the result is clinically important, and is not the probability that a result occurred by chance. An unadjusted p-value also does not account for testing multiple outcomes or comparisons.

Random allocation is intended to make treatment assignment independent of prognostic characteristics, on average, so that outcome differences can be compared across groups. It does not ensure that every characteristic is balanced in a particular trial. The registry reports randomized allocation but does not report the randomization sequence, allocation concealment procedures, or any adjusted analysis. The parallel-group structure means participants were assigned to a group rather than being described as crossing between treatments. The record identifies quadruple masking but does not specify which roles were masked or how masking was maintained.

The stated analysis population for the primary outcome is intent to treat. In general, an intent-to-treat approach analyzes participants according to their assigned group, regardless of treatment adherence, subject to the outcome data and analysis rules. The label alone does not reveal how missing outcome measurements were handled, whether all randomized patients had an observed Week 8 value, or whether exclusions occurred. The registry record does not report those details.

Over-dispersion is relevant to outcomes modeled as counts or rates when variability exceeds what a simple model assumes. General statistical methods may account for it when appropriate. This primary endpoint is a binary percentage, and the registry record does not report use of an over-dispersion model. No such method should be inferred from the posted summary statistics.

The comparisons report simple measures of association and unadjusted p-values. The registry record lists no posted analysis records, while providing the outcome and comparison results; this does not establish the full methods used by the sponsor. The record does not report the original statistical analysis plan, covariate adjustment, multiplicity procedure, missing-data strategy, or interim-analysis plan. Those omissions limit the extent to which the posted comparisons can be connected to any prespecified testing hierarchy or more complex analysis.

10. Confidence Intervals and Precision

The risk-difference confidence interval for dexamethasone 350 µg versus sham is 0.107 to 0.367, around an estimate of 0.237. For dexamethasone 700 µg versus sham, it is 0.216 to 0.482, around an estimate of 0.349. These intervals describe uncertainty in the estimated absolute contrasts. Neither interval includes zero, the value corresponding to no risk difference under this measure.

Interval width is one indication of precision: narrower intervals indicate a more precise estimate, while wider intervals leave more uncertainty about the magnitude. The intervals do not pinpoint a single true effect, and their limits should not be treated as guaranteed bounds. Their interpretation depends on the method and assumptions used to calculate them; the registry record does not report the trial’s interval-construction method.

The posted ratio estimates also have confidence intervals. For the 350 µg comparison, the risk-ratio interval is 1.514 to 5.946 and the odds-ratio interval is 1.772 to 9.498. For 700 µg, the risk-ratio interval is 2.044 to 7.624 and the odds-ratio interval is 2.858 to 14.95. These intervals are on ratio scales, where the null value is 1 rather than zero. Their widths show that the point estimates should not be read as exact values.

Precision applies to the estimates for the stated Week 8 endpoint and comparison. It does not address generalizability, measurement validity, missing-data bias, or multiplicity. The registry record does not report enough detail to assess those issues fully. Confidence intervals also do not indicate whether an observed difference is important to patients or clinicians.

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 figures are planning illustrations, not the trial’s original design calculation. For these binary-outcome comparisons, the reported figures are participants per arm, not total events. The planning assumptions are 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 registry record does not report the assumptions used for the trial’s own original sample-size justification.

For the 350 µg versus sham comparison, planning for 100% of the observed effect gives 50 participants per arm for 80% power and 66 participants per arm for 90% power. Planning for 75% of the observed effect gives 81 participants per arm for 80% power and 108 participants per arm for 90% power. Planning for 50% of the observed effect gives 163 participants per arm for 80% power and 217 participants per arm for 90% power.

For the 700 µg versus sham comparison, planning for 100% of the observed effect gives 26 participants per arm for 80% power and 34 participants per arm for 90% power. Planning for 75% of the observed effect gives 42 participants per arm for 80% power and 56 participants per arm for 90% power. Planning for 50% of the observed effect gives 83 participants per arm for 80% power and 111 participants per arm for 90% power.

The 80% and 90% power columns describe the planned probability of detecting the specified effect under the listed assumptions if that effect were true. A higher target power generally requires more participants for the same effect. Likewise, smaller effects need more participants to detect than larger effects. The curve should be read as a display of this relationship under the same planning framework. These calculations 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 = 0.118; treatment proportion p₁ = 0.355; average p̄ = 0.237.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6012 = 1.1784.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5775 = 0.4860.
4. n = (1.1784 + 0.4860)² / (0.2368)² = 49.4, rounded up to 50 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 <- 0.118421052631579                          # control proportion
p1 <- 0.355263157894737                          # 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(333814)
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 = 50 (80% power), 66 (90% power)
 75% of observed effect: n per arm = 81 (80% power), 108 (90% power)
 50% of observed effect: n per arm = 163 (80% power), 217 (90% power)
power.prop.test: 49.4 
Simulated power at n = 50 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 posts one primary outcome, the percentage of patients with a vitreous haze score of zero at Week 8, and two comparisons against sham. It does not report a multiplicity adjustment, a prespecified testing hierarchy, or how the comparisons were intended to be interpreted together. The reported p-values are unadjusted. When several comparisons or outcomes are tested, the chance of at least one apparently unusual result can increase; general methods can address that issue, but the registry record does not say whether a method was used in the sponsor’s analysis.

The registry lists three outcome measures but no posted secondary outcomes. It also lists zero analysis records. This does not mean that no analysis was conducted, since primary outcome and comparison results are posted; it means the registry record does not include additional analysis records in that listing. Details of any analyses beyond the posted summaries are not reported in the registry record.

The primary outcome is identified as intent to treat. That label gives the intended population framework, but it does not specify how missing Week 8 measurements were treated. The record does not report the number of missing assessments, reasons for missingness, imputation methods, sensitivity analyses, or rules for excluding observations. The arm denominators in the posted comparison data are stated, but they cannot by themselves establish the missing-data process.

The registry record also does not report whether the statistical plan included interim analyses or stopping rules, or whether the posted comparisons were prespecified in the same form. It does not provide the original sample-size justification. These gaps prevent a full assessment of how the reported p-values relate to any planned analysis strategy. They are limitations of the registry information, not evidence that particular procedures were or were not used.

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: retinal detachment (2.7%), cataract (1.4%), necrotising retinitis (1.4%), pupillary disorder (1.4%), small intestinal obstruction (1.4%).

The safety summary reports serious adverse events affecting 6 participants at risk of 74 in the dexamethasone 350 µg group, 7 at risk of 76 in the dexamethasone 700 µg group, and 5 at risk of 75 in the sham group. These are group-specific counts and denominators. They should be read as the registry’s serious adverse event summary, not combined across groups or treated as a comparison adjusted for exposure or follow-up.

The most frequently listed serious-event terms are Retinal Detachment at 2.7%, and Cataract, Necrotising retinitis, Pupillary disorder, Small intestinal obstruction, and HIV test positive at 1.4% each. The registry record does not describe the event-term coding or provide further detail about the circumstances, timing, or relatedness of these events.

Other adverse events are reported as affecting 58 participants at risk of 74 for 350 µg, 61 at risk of 76 for 700 µg, and 51 at risk of 75 for sham. The record does not provide a death count; deaths are not reported in the registry record. These summaries do not establish causation or provide a complete assessment of safety. The registry record does not report a formal statistical comparison for these safety counts.

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

The posted primary outcome shows different Week 8 proportions across the randomized groups: 35.5% with a zero vitreous haze score in the dexamethasone 350 µg arm, 46.8% in the 700 µg arm, and 11.8% in the sham arm. The unadjusted risk-difference estimates and confidence intervals describe the size and uncertainty of each comparison with sham. They indicate that the posted data favor a higher observed proportion meeting this particular endpoint in each dexamethasone group.

This result concerns a specific score threshold at a specific assessment time. It does not describe the full distribution of inflammation scores, the duration of a zero score, or outcomes beyond Week 8. The registry record does not provide posted secondary outcome results, so the primary endpoint cannot stand in for other measures of disease status or functioning.

The results also do not by themselves settle whether differences are clinically important. Statistical evidence, as represented by unadjusted p-values and confidence intervals, is distinct from clinical importance. The registry record does not provide a threshold for a clinically meaningful difference or information that would establish how patients value the endpoint.

Nor do the efficacy summaries alone establish the overall balance of benefit and harm. Serious adverse event counts and other adverse event counts are posted, but the registry does not report enough detail to assess causality, timing, event duration, or a formal comparison of safety. These data should be interpreted as descriptive summaries rather than proof that an event was caused by an intervention.

Finally, interpretation depends on analysis and data-quality details that are not reported in the registry record, including the handling of missing Week 8 assessments and any multiplicity procedure. The findings describe the posted trial results for its stated population and measure; they should not be extended to unreported outcomes, follow-up times, or populations.

16. Why This Trial Matters Statistically

This trial provides a clear example of why the choice of effect measure matters for binary outcomes. The primary result is reported as percentages meeting a threshold, while the comparisons include risk differences, risk ratios, and odds ratios. The risk difference expresses an absolute contrast; the ratios express relative contrasts. Each answers a different statistical question, and the ratio estimates should not be interpreted as absolute changes.

The result also illustrates the role of confidence intervals alongside p-values. The posted comparisons have unadjusted p-values of <0.001, but the intervals add information about the range of estimated differences compatible with the analysis. A p-value alone does not communicate precision or the likely magnitude of an effect. Reading the estimates and intervals together gives a fuller description of the posted statistical evidence.

The two dexamethasone doses are each compared with sham. This makes multiplicity relevant to interpretation, yet the registry record does not report a correction or testing hierarchy. The distinction between unadjusted comparison-level results and a prespecified strategy is important: a statistically small p-value does not resolve how multiple results should be interpreted as a group.

Finally, the record illustrates the boundary between posted results and a complete statistical report. The outcome, groups, comparisons, and safety summaries are available, while details about missing data, covariate adjustment, the original sample-size justification, and the analysis plan are not reported in the registry record. Clear interpretation therefore requires describing what the estimates address while avoiding conclusions about methods or outcomes that the record does not establish.

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 registry record provides arm-level percentages and comparison statistics for the primary endpoint, but does not report the method used to construct the confidence intervals or whether the sponsor’s analysis included adjustment beyond the unadjusted comparisons. It also does not report a multiplicity procedure, despite posting two dose-versus-sham comparisons.

Although the primary outcome is identified as intent to treat, the handling of missing Week 8 assessments is not reported in the registry record. The number of unavailable measurements and any imputation or sensitivity analyses are also not reported. The listed arm denominators do not resolve those questions.

The registry describes quadruple masking but does not identify which roles were masked or explain how the masking was maintained. The randomization implementation, allocation concealment, eligibility details, and any protocol deviations are not described in the posted information. These gaps limit assessment of potential bias and of how closely the reported comparisons follow the intended design.

Only the primary outcome results are posted, with no secondary outcome analyses reported. The Week 8 threshold result does not describe longer-term outcomes or the full distribution of vitreous haze scores. The safety record gives event counts and selected serious-event terms, but does not report event timing, duration, relatedness, or formal statistical comparisons. The original sample-size justification and interim-analysis plan are not reported in the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study of the Safety and Efficacy of a New Treatment for Non-Infectious Intermediate or Posterior Uveitis — NCT00333814.
• Registry record last updated 2011-04-14; status last verified 2011-03.
• Results first posted 2011-04-14.
• 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.

21. Record Summary

NCT00333814 is a completed randomized, quadruple-masked, parallel-group Phase 2 and Phase 3 study sponsored by Allergan. It enrolled 229 participants and compared dexamethasone 350 µg and 700 µg with sham injection for non-infectious intermediate or posterior uveitis. The listed start was 2006-05, and primary completion was 2008-12.

The primary outcome was the percentage of patients with a vitreous haze score of zero at Week 8 in the intent-to-treat population. Posted percentages were 35.5% for 350 µg, 46.8% for 700 µg, and 11.8% for sham. Unadjusted risk differences versus sham were 0.237 and 0.349, respectively; both reported p-values were <0.001.

Serious and other adverse event counts are also posted. The registry record does not report secondary outcome analyses, the trial’s original sample-size justification, missing-data methods, or a multiplicity procedure.