Safety and Efficacy Study of Dexamethasone in the Treatment of Patients With Macular Edema Following Retinal Vein Occlusion (RVO): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of Dexamethasone in the Treatment of Patients With Macular Edema Following Retinal Vein Occlusion (RVO) (NCT01660802), a randomized phase 3 study. The primary outcome is Number of Patients With 15 or More Letter Improvement in Best Corrected Visual Acuity (BCVA) in the Study Eye.

2. Clinical Question

The endpoint uses a threshold on an eye-chart measure: patients either meet the stated improvement threshold or do not. The posted results therefore describe the number of patients who crossed that threshold, rather than the full distribution of changes in visual-acuity letters. The separate secondary outcomes listed in the registry concern average change, change, and the percentage with the same threshold improvement.

This question is about the outcome and comparison recorded for this trial. The registry record does not report enough information to determine how the treatment groups may have differed in other ways, or how the primary result related to any broader clinical decision.

3. Trial Design

The registry describes this as a Phase 3, randomized, parallel-group trial with triple masking. It lists 262 participants as the enrollment. The trial status is completed. The recorded start date is 2012-09-04 and the primary completion date is 2014-03-31.

Participants were assigned to 700 μg dexamethasone or sham. Both were administered in the study eye on Day 1: dexamethasone by intravitreal injection and sham as a sham procedure. The brief summary describes a six-month double-blind period comparing dexamethasone with sham, followed by a two-month open-label period. The registry also lists triple masking as the masking design. The record does not explain how the masking description relates to the wording in the brief summary.

The primary endpoint is reported at baseline and six months. The primary outcome population is modified intent-to-treat, defined in the record as all randomized and treated patients. The arm-level results for this endpoint show 129 patients in the dexamethasone group and 130 in the sham group. The registry record does not explain the relationship between these endpoint counts and the enrollment figure, or give reasons for any difference.

The posted outcomes include the primary responder count and three secondary outcomes related to best corrected visual acuity. The record lists no analyses. It does not report the original statistical analysis plan, sample-size justification, allocation procedure details, or any interim-analysis plan. The sample-size illustrations elsewhere on this page are based on the observed outcome, not the trial's original design.

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: Modified Intent-to-Treat: all randomized and treated patients

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 Number of Patients With 15 or More Letter Improvement in Best Corrected Visual Acuity (BCVA) in the Study Eye, measured over Baseline, 6 Months.

The primary endpoint counts patients whose best corrected visual acuity in the study eye improved by at least 15 letters from baseline to the six-month assessment. The registry describes best corrected visual acuity as measured with an eye chart, with correctly read letters ranging from 0 to 100. More letters read correctly represent better visual acuity.

This is a binary responder outcome: each patient is classified according to whether the improvement threshold was reached. Reporting the number of responders makes the result interpretable as a count and allows the groups to be compared by their observed proportions. It does not show how far each patient's acuity changed, or how changes were distributed among patients who did not meet the threshold.

A threshold outcome can be useful when the research question is framed around reaching a specified amount of improvement. The posted endpoint does not, by itself, establish why this particular threshold was selected or whether it represents a clinically important change for every patient. That rationale is not reported in the registry record.

The registry identifies the primary outcome population as modified intent-to-treat: all randomized and treated patients. The reported timeframe is baseline and six months. This endpoint is distinct from the listed secondary outcomes concerning average change, change from baseline, and the percentage with improvement of at least 15 letters.

7. Results Posted in the Registry

• 700 μg Dexamethasone: 46.5% (60/129) versus 23.8% (31/130) on control; risk difference 22.7 percentage points (95% CI 11.4 to 34.0), risk ratio 1.95 (1.36–2.79); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a binary response, because each patient is counted as either reaching the at-least-15-letter improvement threshold or not reaching it. The posted arm results give the number of responders and the number of patients in each group. Those counts support comparisons based on proportions, such as a risk difference, a risk ratio, and an odds ratio. The registry also gives an unadjusted p-value and an interval for the risk difference.

What does the risk difference describe?

In general, a risk difference subtracts one group's event proportion from the other group's event proportion. For this endpoint, the event is meeting the visual-acuity improvement threshold. The estimate of 0.227 is an absolute contrast between the observed proportions. Its interval, from 0.114 to 0.340, communicates uncertainty in that contrast. Because the risk difference is expressed on an absolute scale, it can be useful for understanding the size of the separation in the observed responder proportions.

How do relative measures differ?

In general, a risk ratio divides one event proportion by another. It describes a relative comparison, so its interpretation depends on the event being compared and the reference group. The reported risk ratio is 1.95, with an interval from 1.363 to 2.792. An odds ratio compares the odds of the event rather than the event proportions. The reported odds ratio is 2.777, with an interval from 1.632 to 4.725. Risk ratios and odds ratios are not absolute differences, and they are not interchangeable with one another.

What does the p-value tell us?

In general, a p-value is calculated under a null hypothesis and a statistical model. It summarizes how unusual data at least as incompatible with that null would be if the null model and its assumptions held. Here, the posted unadjusted p-value is <0.001. It does not quantify the probability that the null is true, the chance that the result will repeat, or the clinical value of the outcome. The registry record does not identify the test used or provide a detailed analysis specification.

Why are the interval and estimate both useful?

An estimate gives a single summary of the observed group contrast. An interval shows that the estimate is not known without uncertainty. In general, a narrower interval indicates greater statistical precision under the chosen method, while a wider interval leaves more uncertainty about the size of the contrast. The interval is not a range containing every individual patient's response. It describes uncertainty about the group-level effect estimate.

What does an unadjusted comparison leave open?

An unadjusted comparison uses the reported outcome data without accounting for covariates in a model. Randomization is the trial's stated allocation design, but the registry record does not report an adjusted analysis or details of baseline balance for this endpoint. The reported unadjusted contrast therefore should not be described as a covariate-adjusted treatment effect. The record lists zero analyses, and the original statistical analysis plan is not reported in the registry record.

Why can a binary endpoint simplify the result?

In general, converting a measurement to a responder classification can make a result easier to describe against a prespecified threshold. It also discards detail: a patient just below the threshold and a patient with little change fall into the same non-responder category, and patients who both cross the threshold may have different amounts of improvement. The registry also lists secondary outcomes about average change and change from baseline, but their numerical results are not included. The posted primary result should therefore be interpreted as a threshold-based summary rather than a complete description of visual-acuity changes.

For outcomes counted as events, variation can be affected by the underlying event frequency and the number of participants. General statistical methods may use different assumptions to calculate intervals or tests. The precise method behind these posted figures is not reported in the registry record, so the numerical outputs should be described as posted rather than attributed to a method the record does not identify.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.227, and the interval shown for it runs from 0.114 to 0.340. This interval describes uncertainty in the estimated absolute difference between the groups' responder proportions. It should be read together with the point estimate: the estimate gives one summary, while the interval shows a range of values compatible with the calculation and data under its assumptions.

The interval lies above zero, meaning that the range displayed does not include no difference on the risk-difference scale. This is consistent with the posted unadjusted p-value of <0.001. Neither the interval nor the p-value proves a particular explanation for the observed group separation. Both depend on the data and statistical procedure, and the procedure's detailed specification is not reported in the registry record.

The relative estimates also have intervals: 1.95 for the risk ratio, with an interval from 1.363 to 2.792, and 2.777 for the odds ratio, with an interval from 1.632 to 4.725. These intervals are on different scales and answer different descriptive questions. They should not be compared numerically with the risk-difference interval as though all three shared the same units.

Precision is not the same as certainty, and an interval does not show the distribution of individual responses. The registry does not state the confidence level associated with these intervals in the record. Their interpretation should therefore stay with the stated estimates and endpoints, without attaching an unreported confidence level.

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 effect, not the original trial design. The table reports participants per arm, not total events. Its scenarios use 100%, 75%, and 50% of the observed effect. For each scenario, the table gives the number of participants per arm for 80% power and the number of participants per arm for 90% power.

The listed 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 the stated fraction of the observed effect. The trial's original sample-size justification and design assumptions are not reported in the registry record.

In plain terms, the 80% power column gives the planned participants per arm for a design with an 80% chance of detecting the assumed effect under the stated assumptions. The 90% power column gives the corresponding planning number for a 90% chance. These are design properties conditional on the assumptions, not guarantees that a study will detect an effect.

For 100% of the observed effect, The table shows 69 participants per arm for 80% power and 92 for 90% power. For 75% of the observed effect, it lists 118 and 158 participants per arm. For 50% of the observed effect, it lists 254 and 339 participants per arm. Smaller effects need more participants to detect under these assumptions. This is 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 = 0.238; treatment proportion p₁ = 0.465; average p̄ = 0.352.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6753 = 1.3236.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6560 = 0.5521.
4. n = (1.3236 + 0.5521)² / (0.2267)² = 68.5, rounded up to 69 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 <- 0.238461538461538                          # control proportion
p1 <- 0.465116279069767                          # 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(1660802)
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 = 69 (80% power), 92 (90% power)
 75% of observed effect: n per arm = 118 (80% power), 158 (90% power)
 50% of observed effect: n per arm = 254 (80% power), 339 (90% power)
power.prop.test: 68.5 
Simulated power at n = 69 per arm: 0.804 (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 lists four outcome measures in total and three secondary outcomes. The secondary measures concern average change from baseline in best corrected visual acuity, change from baseline in best corrected visual acuity, and the percentage of patients with at least a 15-letter improvement. The primary endpoint is also a responder outcome based on that improvement threshold.

When several outcomes or analyses are examined, the chance of obtaining at least one apparently notable result can increase if no adjustment or prespecified hierarchy is used. In general, multiplicity procedures address this issue by controlling how results are interpreted across a family of tests. The registry record does not report a multiplicity strategy, an endpoint hierarchy, or which outcomes were designated for confirmatory inference beyond identifying the primary outcome.

The registry lists zero analyses. It therefore does not provide analysis details such as a complete model specification, covariate adjustment, or a reported sensitivity analysis. The primary comparison is unadjusted. It is not possible from this record to establish whether other analyses were conducted outside the posted registry results.

The endpoint population is described as modified intent-to-treat: all randomized and treated patients. The record does not report how missing six-month measurements were handled, how many outcome observations were missing, or whether any imputation or sensitivity analyses were used. It also does not explain exclusions from the endpoint population. These omissions limit assessment of whether missing information could affect the comparison.

The registry record does not report interim analyses or stopping rules. These details should not be inferred from the trial's status or the posted p-value. Without the analysis plan and missing-data details, the result can be summarized as the posted comparison for the stated population, while leaving these aspects of the analysis 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: atrioventricular block (0.8%), cholecystitis chronic (0.8%), vitreous haemorrhage (0.8%).

The serious adverse event figures show 1 affected patient among 129 in the 700 μg dexamethasone group and 2 among 130 in the sham group. The registry also reports other adverse events affecting 69 among 129 in the dexamethasone group and 15 among 130 in the sham group. These are counts of affected patients as represented in the posted safety fields; they are not the primary efficacy endpoint.

The record lists Atrioventricular Block, Cholecystitis Chronic, and Vitreous Haemorrhage among the top serious adverse event terms, each shown as 0.8%. These entries describe reported terms and their listed percentages. The registry record does not provide further detail about event timing, severity, recurrence, or attribution to study treatment. A reported adverse event does not by itself establish that the intervention caused it.

Death counts are not reported in the registry record. The safety figures should be read as a summary of the posted counts, not as a complete assessment of all possible harms or as a comparison adjusted for differences in exposure or follow-up.

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

The posted primary outcome shows a difference between the groups in the number of patients meeting the at-least-15-letter improvement threshold at six months. There were 60 responders among 129 patients in the 700 μg dexamethasone group and 31 among 130 patients in the sham group. The estimated unadjusted risk difference is 0.227, with an interval from 0.114 to 0.340, and the posted p-value is <0.001.

This result describes the trial's responder endpoint in its modified intent-to-treat population. It does not describe every patient's change in visual acuity, because patients are grouped according to whether they crossed the threshold. It also does not establish that all patients in one group had a similar response or that the observed difference applies to populations not represented by this trial.

The result does not, by itself, establish why the groups differed or quantify the overall balance of benefits and harms. The registry's safety section includes adverse-event counts, but the posted information does not establish causation or provide a complete safety assessment. The listed secondary outcomes have no numerical results in the record.

The registry summary describes an open-label period after the six-month double-blind period, but the primary result is tied to baseline and six months. It should not be extended to later outcomes that are not reported. The record also does not report the full statistical analysis plan, missing-data methods, multiplicity strategy, or the original sample-size rationale. Those absences limit how fully the analysis can be evaluated.

In short, the posted data show more patients in the dexamethasone arm met the specified responder threshold than in the sham arm, with the reported group-level estimate and uncertainty. This is a statistical summary of the registry result, not medical advice or a complete account of the trial.

16. Why This Trial Matters Statistically

This trial illustrates why it is useful to distinguish a responder count from a continuous measurement. The primary endpoint turns eye-chart change into a threshold-based outcome: patients are counted if their improvement reaches at least 15 letters. That makes the result straightforward to express as group counts and proportions, while leaving out detail about the size of changes within each response category.

It also shows why absolute and relative effect measures should be read separately. The risk difference of 0.227 describes an absolute group contrast, while the risk ratio of 1.95 and odds ratio of 2.777 express relative comparisons on different scales. Each provides a different view of the same endpoint and should be interpreted with its own interval.

The interval around the risk difference is important alongside the point estimate. It conveys uncertainty about the size of the group contrast, while the p-value addresses compatibility with a null model under the test assumptions. Neither number substitutes for the other, and neither alone establishes clinical importance.

Finally, the record highlights the distinction between trial design information and a retrospective planning illustration. The planning table uses fractions of the observed effect and stated assumptions. It cannot stand in for the original design rationale, which is not reported in the registry record. Together, these features make the trial a useful example of how endpoint definition, effect scale, precision, and reporting completeness shape statistical interpretation.

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.

The registry enrollment is 262, while the primary endpoint arm counts are 129 and 130. The record does not explain this difference or report the reasons for any patients not represented in the endpoint counts. It identifies the endpoint population as all randomized and treated patients, but does not provide further details about treatment exposure or the handling of participants without an endpoint measurement.

The primary result is a six-month threshold-based outcome. It does not provide the full distribution of letter changes, and numerical results for the listed secondary visual-acuity outcomes are not included. The brief summary mentions a two-month open-label period after the six-month double-blind period, but later outcome results are not reported in this record.

The record does not report the original sample-size calculation, the statistical analysis plan, a detailed analysis method, multiplicity handling, interim analyses, or missing-data procedures. It lists zero analyses. As a result, the posted unadjusted comparison cannot be evaluated against a complete prespecified analysis framework using this information alone.

The safety summary provides affected-patient counts and selected serious adverse event terms, but not fuller details about timing, severity, exposure, or attribution. Death counts are not reported in the registry record. These limitations concern what can be concluded from the posted information; they do not establish that unreported procedures or analyses were absent from the trial.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of Dexamethasone in the Treatment of Patients With Macular Edema Following Retinal Vein Occlusion (RVO) — NCT01660802.
• Registry record last updated 2019-04-17; status last verified 2019-04.
• Results first posted 2015-06-08.
• 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

The registry describes a completed Phase 3 randomized, triple-masked, parallel-group trial of 700 μg dexamethasone versus sham in patients with macular edema following retinal vein occlusion. The brief summary describes a six-month double-blind comparison followed by a two-month open-label period. Enrollment is listed as 262.

The primary outcome counts patients with at least a 15-letter improvement in best corrected visual acuity in the study eye at six months. The registry reports 60 of 129 patients in the dexamethasone group and 31 of 130 in the sham group, with an unadjusted risk difference of 0.227 and p-value <0.001. The endpoint population is described as modified intent-to-treat: all randomized and treated patients.

The record lists three secondary outcomes, zero analyses, and selected adverse-event counts. It does not report the original sample-size rationale, detailed statistical analysis plan, multiplicity procedures, or missing-data methods.