A 3-Month Clinical Trial to Assess the Safety and Efficacy of the OZURDEX® Intraocular Implant in Patients With Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A 3-Month Clinical Trial to Assess the Safety and Efficacy of the OZURDEX® Intraocular Implant in Patients With Diabetes Mellitus (NCT01673191), a randomized phase 2 study. The primary outcome is Mean Change in Best Corrected Visual Acuity.

2. Clinical Question

The outcome is a measure of visual acuity, not a direct measure of macular edema itself. The registry reports group mean changes and a contrast between the arm means. The contrast is unadjusted, and its confidence interval is broad enough to include values on either side of no difference. The posted data therefore describe the observed results and their uncertainty; they do not establish a definitive difference between treatment groups.

The registry labels allocation as randomized, but also labels the study model as single group. It lists two interventions and posts results for two arms. Those entries do not fully clarify the intended comparison structure. Additional information about eligibility, treatment assignment, and analysis populations is not reported in the registry record.

3. Trial Design

NCT01673191 is listed as a completed Phase 2 trial sponsored by Retinal Consultants of Arizona. Its title describes a 3-month clinical trial of the OZURDEX intraocular implant in patients with diabetes mellitus. The registry lists an enrollment of 40 and a study start of 2012-11, with primary completion in 2014-12.

The record identifies the allocation as randomized and masking as none. It also labels the model as single group, while listing two interventions and reporting results for two arms: the DEX implant arm and the topical steroid/NSAID arm. The record does not explain this difference in labels, so the design should not be reconstructed beyond what is explicitly listed. No details about the randomization procedure, treatment assignment, or whether participants or assessors knew treatment assignment are reported beyond the no-masking entry.

The listed interventions are a dexamethasone intravitreal implant and steroid plus NSAID eye drop combination therapy. The arm description identifies the implant as OZURDEX, 0.7 mg, and the topical regimen as Acular LS and Pred Forte. The primary outcome is mean change in best corrected visual acuity, in logMAR units, at 1 months. Although the title describes a 3-month trial, the primary outcome timeframe is listed as 1 months.

The registry lists an enrollment of 40, while the posted primary outcome summaries give 26 participants for the DEX implant arm and 11 for the topical steroid/NSAID arm. The record does not explain the relationship between the enrollment figure and the numbers included in these summaries. Reasons for any difference, and details of follow-up or analysis eligibility, are not reported in the registry record.

The original protocol, planned sample-size justification, and full statistical analysis plan are not reported in the registry record. The posted arm summaries and comparison can be interpreted as results recorded for this trial, but they do not provide enough information to verify all aspects of its design or analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Mean Change in Best Corrected Visual Acuity, measured over 1 months.

The primary endpoint is mean change in best corrected visual acuity, measured in logMAR units. Best corrected visual acuity measures how clearly a participant can see when refractive correction is applied. LogMAR is a logarithmic scale commonly used to express visual acuity. As a general interpretation of the scale, lower logMAR values correspond to better visual acuity; however, the registry record does not specify the sign convention used for calculating the reported change from baseline.

A change endpoint compares a follow-up measurement with a baseline measurement. Reporting the mean change describes the average change among participants included in each arm’s summary. It does not show how every participant changed: individual responses can vary, and the standard deviation describes the spread of observed changes around the arm mean.

The primary outcome timeframe is listed as 1 months. The DEX implant arm has a reported mean change of 0.3 logMAR units and a standard deviation of 0.2. The topical steroid/NSAID arm has a mean change of 0.33 logMAR units and a standard deviation of 0.37. The registry does not provide additional detail about the baseline values, measurement schedule, or handling of missing endpoint measurements.

Visual acuity is relevant to the stated clinical context, but this endpoint alone does not describe every aspect of macular edema, eye health, or treatment safety. Interpretation should remain tied to the measured outcome, the specified timeframe, and the uncertainty around the comparison.

7. Results Posted in the Registry

• Topical Steroid/NSAID ARM: mean 0.33 versus 0.30 on control; difference 0.03 (95% CI -0.20 to 0.26), standardized effect d = 0.12; z-test p = 0.800.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: it is a numerical measure that can take a range of values. The registry reports a mean and standard deviation for each arm. These statistics answer different questions. The mean summarizes the average change in the arm, while the standard deviation describes how dispersed participant measurements were around that average. A standard deviation is not a confidence interval and does not, by itself, express how precisely the mean or the difference between means has been estimated.

What does the mean difference represent?

The posted comparison expresses the difference between the two arm means in logMAR units. Its estimate is 0.03, comparing the topical steroid/NSAID arm with the DEX implant arm. This is a contrast of group averages, not a count of participants who improved, a proportion reaching a threshold, or a measure of an individual participant’s response. The registry does not report a threshold defining a clinically important change.

The arm summaries also include standard deviations: 0.2 for the DEX implant arm and 0.37 for the topical steroid/NSAID arm. Variation matters because participants’ measurements may differ from their arm’s mean. Greater spread can make a mean less precisely estimated when the number of observations is limited. The record does not give participant-level observations, so the distribution of changes and the presence of unusual values cannot be assessed from these summaries alone.

How should the confidence interval be read?

A confidence interval describes uncertainty around an estimate under the statistical procedure used to construct it. In general, a wider interval indicates less precision than a narrower interval. The posted interval for the mean difference crosses zero, so values consistent with the interval include differences in either direction as well as no difference. It therefore conveys more than the point estimate alone: the arm means are close in the posted estimate, but the uncertainty permits a range of contrasts.

The registry record does not identify the method used to construct this confidence interval or state whether it was prespecified. The interval should be read as the uncertainty range posted alongside the comparison, not as a guarantee about the true difference or as proof that every value in the interval is equally plausible.

What does the p-value say?

The unadjusted p-value is 0.8. In general, a p-value measures how compatible observed data are with a specified statistical null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, the probability that chance alone produced the result, or a measure of clinical importance. A comparatively large p-value does not establish equivalence, and it does not show that the true effect is zero.

The record does not identify the test used to produce the posted p-value or describe its assumptions. It is therefore appropriate to report it as an unadjusted p-value without inferring details of the analysis procedure. The registry lists randomized allocation, but the single-group model label and the two reported arms make it especially important not to infer unrecorded analysis details.

Why does variability matter?

When outcomes vary more among participants, an arm mean can be less precise for a given amount of information. This is one reason that the standard deviations are useful alongside the means. The topical arm’s standard deviation is 0.37, while the DEX implant arm’s is 0.2. The sizes of the arm summaries are 11 and 26, respectively. Those differing counts and spreads help explain why the point estimate should be read together with its confidence interval rather than in isolation.

General statistical methods may also account for over-dispersion, which means that observed variability is greater than a model expects. That concept is relevant in some analyses, but the record does not report an over-dispersion assessment or identify a model that would require one. No such procedure should be assumed for this comparison.

What can be inferred about the analysis?

The registry lists seven outcome measures and no secondary outcomes posted. It lists zero analyses. This means there is no separate analysis record described in the registry entry, even though arm summaries and a comparison are posted. The original statistical plan, prespecified model, analysis population, handling of missing measurements, and multiplicity strategy are not reported in the registry record. Without those details, the posted summary cannot establish whether the reported analysis followed a prespecified plan or how all planned outcomes were treated.

The arm-specific counts for the primary result are 26 and 11, whereas the listed enrollment is 40. This difference is visible in the record, but no explanation is given. It is not possible from the posted information to identify how many enrolled participants lacked an endpoint measurement, whether any participants were excluded, or why the counts differ.

The sample-size illustrations use a normal approximation, equal allocation between two arms, a two-sided significance level of 0.05, and effects set to stated fractions of the observed effect. These are planning assumptions for the illustration, not evidence of the methods used in the completed trial. The original design assumptions and sample-size justification are not reported in the registry record.

10. Confidence Intervals and Precision

The point estimate for the unadjusted mean difference is 0.03 logMAR units, comparing the topical steroid/NSAID arm with the DEX implant arm. The confidence interval crosses zero, extending to both negative and positive possible differences. This means the estimate is not precise enough to distinguish clearly between a difference favoring either direction and no difference, based on the posted interval.

A confidence interval gives a range of estimates compatible with the observed data under the procedure used to calculate it. It is not a range containing every participant’s result, and it does not guarantee that the true difference lies within its limits. A narrow interval would indicate greater precision; a broad interval would indicate that the data leave more uncertainty. The interval posted for this comparison is broad relative to the point estimate and includes zero.

The unequal arm counts contribute context for reading precision: 26 participants are included in the DEX implant summary and 11 in the topical steroid/NSAID summary. The standard deviations are 0.2 and 0.37, respectively. These values indicate variability in the measured changes, but do not replace the interval for the between-arm comparison. In particular, the point estimate alone should not be treated as a precise estimate of the contrast.

The unadjusted p-value is 0.8, which is consistent with the interval’s inclusion of zero. Neither statistic proves that the arms are the same. The registry does not report a prespecified equivalence margin or noninferiority margin, so the results cannot be interpreted as demonstrating equivalence or noninferiority. Details of the interval construction and analysis plan are not reported in the registry record.

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 expressed as participants per arm, not total event counts. They use the observed effect as a starting point and consider planning for 100% of that observed effect, 75% of the observed effect, and 50% of the observed effect. For each scenario, the display gives participant counts per arm for 80% power and for 90% power. The 80% power column represents the planning count associated with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and those assumptions were correct. The 90% column represents the corresponding count for a 90% chance.

The illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These are assumptions for the planning illustration; the original trial’s sample-size assumptions and justification are not reported in the registry record.

For planning an effect of 100% of the observed effect, the figures are 1,181 participants per arm for 80% power and 1,581 participants per arm for 90% power. For planning an effect of 75% of the observed effect, the figures are 2,099 participants per arm for 80% power and 2,810 participants per arm for 90% power. For planning an effect of 50% of the observed effect, the figures are 4,723 participants per arm for 80% power and 6,322 participants per arm for 90% power.

The pattern illustrates a general planning principle: smaller effects need more participants to detect, all else equal. The curve gives a visual representation of this relationship, while the listed values show the corresponding planning counts. These figures are not observed power and do not describe the probability that this completed trial found a result. They are planning illustrations based on the observed effect, not the trial’s original design.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.030; pooled standard deviation σ = 0.260.
2. n = 2 × (1.96 + 0.842)² × 0.260² / 0.030² = 1,180.6, rounded up to 1,181 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
delta <- 0.03                      # observed difference in means
sigma <- 0.260164782946721                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1673191)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,181 (80% power), 1,581 (90% power)
 75% of observed effect: n per arm = 2,099 (80% power), 2,810 (90% power)
 50% of observed effect: n per arm = 4,723 (80% power), 6,322 (90% power)
power.t.test: 1181.5 
Simulated power at n = 1,181 per arm: 0.796 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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

Multiplicity arises when a study evaluates multiple outcomes, timepoints, or comparisons. If many statistical tests are performed, the chance of at least one apparently notable result can increase unless the analysis plan addresses that issue. General approaches include designating a primary outcome in advance, adjusting inference across multiple tests, or treating secondary analyses as exploratory. Which approach is suitable depends on the study design and questions.

The registry identifies mean change in best corrected visual acuity at 1 months as the primary outcome. It lists seven outcome measures, but no secondary outcomes are posted and no analyses are listed. The record does not describe whether multiple outcomes or timepoints were planned, whether any multiplicity adjustment was used, or whether the posted primary outcome was selected before results were examined. A formal multiplicity strategy is not reported in the registry record.

Missing-data handling is also not reported. The primary outcome summaries include 26 participants in the DEX implant arm and 11 in the topical steroid/NSAID arm, while enrollment is listed as 40. The registry does not explain this difference. It does not state how many participants had missing measurements, whether participants withdrew, whether observations were excluded, or how missing values were treated in the analysis. Consequently, the possible influence of missing data on the reported means and comparison cannot be assessed from the record.

The analysis population is not reported in the registry record. The entry does not state whether the summary includes all randomized participants, participants who received treatment, participants with available outcome measurements, or another defined group. The randomized allocation label alone does not identify the population used for the posted results.

These gaps do not show that a particular procedure was or was not used. They mean that the registry record does not provide enough information to evaluate multiplicity control, missing-data assumptions, or the relationship between the analyzed participants and all enrolled participants. Those questions require a fuller statistical plan or report.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse event counts of 0 among 26 participants at risk in the DEX implant arm and 0 among 11 participants at risk in the topical steroid/NSAID arm. Deaths are listed as 0 in both arms. The serious adverse event terms list is empty.

For other adverse events, the record lists 1 among 26 participants at risk in the DEX implant arm and 0 among 11 participants at risk in the topical steroid/NSAID arm. These are event counts as recorded, not a comparison adjusted for differences between groups. The record does not provide additional detail about event type, timing, severity, or how events were assessed. The listed counts should not be treated as evidence that no unlisted events occurred or as a complete assessment of safety beyond the registry entries.

Adverse-event counts do not by themselves establish whether an event was caused by treatment. They also do not determine whether risks differ between arms, particularly with the small reported group sizes. The figures describe what the registry record lists for the reported at-risk groups.

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

The posted primary result shows mean changes in best corrected visual acuity of 0.3 logMAR units in the DEX implant arm and 0.33 logMAR units in the topical steroid/NSAID arm at 1 months. The unadjusted mean difference is 0.03 logMAR units. Its confidence interval crosses zero, and the unadjusted p-value is 0.8. The data therefore do not clearly distinguish the arm means statistically, while leaving uncertainty about the size and direction of the difference.

This finding is not proof that the two approaches are equivalent, nor does it establish that any difference is absent. Equivalence requires a prespecified margin and an analysis designed to assess whether the range of plausible effects falls within that margin. Neither an equivalence margin nor a noninferiority margin is reported in the registry record. Likewise, a nonsignificant result does not establish that either approach is ineffective.

The mean change values alone do not establish whether visual acuity improved or worsened, because the registry does not state the direction used when calculating change. General interpretation of logMAR is that lower values correspond to better visual acuity, but the sign convention for this change endpoint is not given. The results should therefore be described as reported mean changes rather than given an unsupported direction.

The results concern the specific endpoint and timeframe listed in the record. They do not establish outcomes for other measures, longer follow-up, other patient groups, or other treatment settings. The registry’s two-arm results, randomized allocation label, and single-group model label also leave some design details unclear. The numbers describe the posted record and should not be extended beyond it.

The adverse-event entries list no serious events or deaths in either arm, and one other adverse event in the DEX implant arm. These counts are descriptive and do not establish comparative safety or causal attribution. The limited detail and group sizes restrict what can be concluded from them.

16. Why This Trial Matters Statistically

This record is statistically informative because it puts an arm-level estimate beside an uncertainty interval and an unadjusted p-value. A point estimate alone can appear more definitive than the data warrant. Here, the interval crosses zero, making clear that the observed difference of 0.03 is not a precise separation between the reported arm means. Reading the interval alongside the estimate avoids treating a single number as the whole result.

The posted arm summaries also show why sample size and variability matter. The primary outcome summaries include 26 participants in one arm and 11 in the other, with standard deviations of 0.2 and 0.37. Small amounts of data, unequal arm counts, and variation in participant measurements can leave substantial uncertainty. The planning illustrations make the broader point that detecting smaller effects generally requires more participants, under a fixed set of planning assumptions.

Equally important is the distinction between a completed trial’s observed result and a planning exercise. The sample-size figures are not observed power and are not evidence about the trial’s original design rationale. The trial’s original sample-size assumptions are not reported in the registry record. Keeping those ideas separate prevents retrospective calculations from being mistaken for an explanation of why the trial enrolled its listed number of participants.

Finally, statistical interpretation depends on design and analysis details, not just numerical output. The record’s randomized allocation and single-group model labels do not align straightforwardly with its two reported arms. The analysis population, missing-data approach, and multiplicity plan are not reported. These limitations illustrate why transparent reporting of design, outcome definitions, and analysis procedures is essential for judging how much weight to place on an estimate.

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.

Several limitations specific to this trial record affect interpretation. First, the title describes a 3-month trial, while the primary outcome timeframe is listed as 1 months. The registry does not explain the relationship between those timeframes or report additional timing details for the primary measurement.

Second, key design labels are difficult to reconcile: allocation is listed as randomized, the model as single group, and results are posted for two arms. The registry does not clarify the assignment procedure or provide enough information to resolve the discrepancy. Masking is listed as none, and further detail about who knew treatment assignment is not reported.

Third, the listed enrollment is 40, but the primary outcome summaries include 26 participants in the DEX implant arm and 11 in the topical steroid/NSAID arm. The record does not explain the difference or identify the analysis population. It also does not report how missing outcome measurements were handled, so the possible impact of missingness cannot be assessed.

Fourth, the primary outcome is reported at a single listed timeframe, and its change-score sign convention is not stated. The record gives no baseline values, no clinically important threshold, and no explanation of whether the endpoint was analyzed as prespecified. The original sample-size justification, statistical analysis plan, and multiplicity strategy are also not reported.

Finally, adverse-event entries provide limited detail, and the arm sizes are small. The registry lists counts but not event timing, descriptions beyond the serious-event category, or an assessment of causal relation. These limitations call for a cautious reading of both the efficacy summaries and the safety entries.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A 3-Month Clinical Trial to Assess the Safety and Efficacy of the OZURDEX® Intraocular Implant in Patients With Diabetes Mellitus — NCT01673191.
• Registry record last updated 2017-04-05; status last verified 2017-02.
• Results first posted 2017-04-05.
• 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

NCT01673191 is a completed Phase 2 registry record sponsored by Retinal Consultants of Arizona, with listed enrollment of 40. Its title describes a 3-month clinical trial in patients with diabetes mellitus. The record lists randomized allocation, no masking, and a single-group model, while also posting results for a DEX implant arm and a topical steroid/NSAID arm.

The primary outcome is mean change in best corrected visual acuity, in logMAR units, at 1 months. The posted means are 0.3 in the DEX implant arm and 0.33 in the topical steroid/NSAID arm. The unadjusted mean difference is 0.03, with a confidence interval crossing zero and an unadjusted p-value of 0.8.

Serious adverse event counts and deaths are listed as 0 in both arms. One other adverse event is listed in the DEX implant arm and none in the topical arm. Details of the original analysis plan, analysis population, missing-data handling, and sample-size justification are not reported in the registry record.