Safety and Efficacy of a New Treatment in Combination With Laser for Diabetic Macular Edema: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of a New Treatment in Combination With Laser for Diabetic Macular Edema (NCT00464685), a randomized phase 2 study. The primary outcome is Percentage of Patients With at Least 10 Letters of Improvement in Best Corrected Visual Acuity (BCVA) From Baseline in the Study Eye.

2. Clinical Question

3. Trial Design

This was a randomized, triple-masked, parallel-group phase 2 trial of treatment for diabetic macular edema. The registry lists an enrollment of 253. Participants were assigned to dexamethasone implant plus laser photocoagulation or sham implant plus laser photocoagulation. Both groups therefore received laser treatment; the contrast concerns adding the dexamethasone implant rather than comparing laser with no treatment.

The registry describes an initial 700 µg dexamethasone implant, with up to 1 additional treatment based on re-treatment criteria. The comparison regimen used an initial sham injection, also with up to 1 additional treatment based on re-treatment criteria. In each group, laser photocoagulation began with an initial treatment and could be given up to 3 additional times based on re-treatment criteria. The record does not report the specific criteria used to determine retreatment.

The listed study start date is 2007-05-01, primary completion date is 2010-02-08, and status is completed. The primary outcome was assessed from baseline to Month 12 in the study eye. Secondary outcomes listed in the registry concern change in BCVA, central subfield retinal thickness, focal leakage area, and time to retreatment.

Details such as the randomization method, allocation concealment, masking procedures, and analysis plan are not reported in the registry record. The record also does not report the trial's original sample-size assumptions or justification. Those omissions limit what can be inferred about how the trial was designed to control bias or how its planned precision related to the observed result.

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: all randomized 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 Percentage of Patients With at Least 10 Letters of Improvement in Best Corrected Visual Acuity (BCVA) From Baseline in the Study Eye, measured over Baseline, Month 12.

The primary endpoint was the percentage of participants with at least 10 letters of improvement in best corrected visual acuity (BCVA) from baseline in the study eye, assessed at Month 12. BCVA was measured with an eye chart and recorded as the number of letters read correctly. The registry explains that a higher letter count indicates better visual acuity, while a decrease indicates worsening.

This endpoint turns change in a continuous letter score into a binary outcome: each participant either met the threshold of at least 10 letters of improvement or did not. Reporting the percentage meeting that threshold gives a direct description of how common that degree of improvement was in each randomized group. The threshold also makes the outcome interpretable as a proportion rather than only as an average change in score.

As a general statistical point, converting a continuous measure into a yes-or-no outcome can make a threshold-based result easier to communicate, but it does not describe the full range of individual changes. Participants just below the threshold and participants with no change fall into the same outcome category, although their score changes may differ. The posted primary result therefore addresses the specified threshold, not every possible pattern of visual-acuity change.

The registry identifies the primary outcome population as all randomized patients. It does not report how missing Month 12 measurements were handled or whether any participants lacked an evaluable BCVA result.

7. Results Posted in the Registry

• 700 µg Dexamethasone Implant and Laser Photocoagulation: 27.8% (35/126) versus 23.6% (30/127) on control; risk difference 4.2 percentage points (95% CI -6.6 to 14.9), risk ratio 1.18 (0.77–1.79); unadjusted two-proportion z-test p = 0.449.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary result is a comparison of proportions: within each randomized group, the proportion of participants who met the specified BCVA improvement threshold was reported. The posted values are 27.8% and 23.6%. A proportion gives the frequency of a defined event in a group; it does not show the distribution of all individual outcome values.

What does the risk difference express?

The risk difference is the difference between the event proportions in the two groups, expressed on the probability scale. The posted unadjusted estimate is 0.042. A value of zero on this scale represents equal event proportions. Its confidence interval extends from -0.066 to a positive upper bound, so it includes zero. This is why the point estimate alone should not be read as a settled group difference: estimates can vary from sample to sample, and the interval represents uncertainty under the method used to calculate it.

The risk difference is an absolute measure. It addresses how far apart the proportions are, rather than expressing one group's event rate as a multiple of the other's. The registry also reports relative measures, but they answer the comparison on different scales. A risk ratio compares proportions as a ratio, while an odds ratio compares odds. Because these measures have distinct interpretations, they are not interchangeable; all require attention to their uncertainty intervals.

What does the p-value tell the reader?

The unadjusted p-value is 0.449. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the statistical procedure. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. The registry does not report a complete analysis plan, so the p-value should be understood as an unadjusted comparison rather than as a full account of the original trial's inferential procedures.

As a general concept, a conventional significance threshold is a decision rule chosen before looking at results. The sample-size planning assumptions mention a two-sided significance level of 0.05, but the registry record does not report whether that threshold governed the trial's primary analysis. A p-value should therefore be interpreted alongside the effect estimate, its confidence interval, and the completeness of the analysis information.

Why are confidence intervals important?

A confidence interval gives a range of estimates compatible with the data under a statistical method and its assumptions. It communicates precision: a narrow interval indicates more precise estimation than a wide interval. For this comparison, the risk-difference interval includes negative, zero, and positive values. That range means the posted estimate does not pin down the direction of the underlying difference with precision. A confidence interval is not a guarantee that a particular range contains the true value, and it does not account automatically for design or reporting limitations.

What does unadjusted mean?

An unadjusted comparison uses the posted group summaries without accounting for additional covariates in a model. This can be a straightforward way to describe the randomized-group contrast, but the result does not show whether an adjusted analysis would differ. The registry does not report covariate-adjusted estimates, a regression model, or other details of the sponsor's analysis. The comparison estimates should thus be read as unadjusted summaries rather than as evidence about any unreported adjusted procedure.

More generally, when a binary endpoint is common enough to occur in both groups, the choice among risk difference, risk ratio, and odds ratio affects how the contrast is expressed. The general statistical point is that readers should identify the scale before interpreting the estimate. Here, the risk difference is the most direct absolute comparison, while the ratio measures provide relative comparisons. None should be considered in isolation from the reported uncertainty.

10. Confidence Intervals and Precision

Precision describes how tightly the data estimate a group contrast. For the primary risk difference, the posted estimate is 0.042, and the confidence interval runs from -0.066 to a positive upper bound. The interval crosses zero, the value corresponding to no risk difference. It therefore includes estimates consistent with a difference favoring either group as well as no difference. This wide range of compatible values limits how specifically the observed group percentages can be generalized.

The relative estimates also have intervals that include their respective no-difference values: 1 for a risk ratio and 1 for an odds ratio. The risk ratio estimate is 1.176, with bounds 0.772 and 1.791. The odds ratio estimate is 1.244, with bounds 0.707 and 2.189. These intervals reinforce that the posted comparison is not precise enough to establish a clear relative separation between groups.

In general, confidence intervals reflect sampling uncertainty under the calculation method. They do not correct for missing outcome data, unreported analysis choices, or other sources of bias. The registry record does not report a missing-data method or detailed primary analysis method, so the displayed interval should be interpreted with those reporting gaps in mind.

Precision is distinct from whether an estimate is clinically important. The registry record does not establish a threshold for a clinically important difference, and the interval alone cannot determine that question. It does show that the primary comparative estimate remains uncertain across a range that includes no difference.

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 based on fractions of the observed effect, not counts of participants observed in the trial. The listed values are participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial's own original design assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 1,735 participants per arm for 80% power and 2,322 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 3,044 participants per arm for 80% power and 4,074 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 6,754 participants per arm for 80% power and 9,042 participants per arm for 90% power.

In plain language, the 80% power column describes a planning target for the chance of detecting the chosen effect under the stated assumptions, if that effect is present. The 90% column uses a higher target and therefore requires more participants per arm in these illustrations. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. These figures are not observed power and should not be read as a retrospective measure of how likely the completed trial was to find a result.

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 = 0.236; treatment proportion p₁ = 0.278; average p̄ = 0.257.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6180 = 1.2112.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6173 = 0.5195.
4. n = (1.2112 + 0.5195)² / (0.0416)² = 1,734.5, rounded up to 1,735 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 <- 0.236220472440945                          # control proportion
p1 <- 0.277777777777778                          # 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(464685)
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 = 1,735 (80% power), 2,322 (90% power)
 75% of observed effect: n per arm = 3,044 (80% power), 4,074 (90% power)
 50% of observed effect: n per arm = 6,754 (80% power), 9,042 (90% power)
power.prop.test: 1734.5 
Simulated power at n = 1,735 per arm: 0.798 (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 the primary binary BCVA outcome and four secondary outcomes: change from baseline in BCVA, change from baseline in central subfield retinal thickness, change from baseline in focal leakage area, and time to retreatment. The secondary outcomes describe different clinical measurements and an event-timing measure. Their analysis results are not reported in the registry record.

When a study evaluates several outcomes or makes several comparisons, the chance of at least one apparently unusual result can increase. As a general statistical principle, multiplicity procedures can address this issue by controlling a chosen error rate across a family of tests. The registry record does not report whether any multiplicity adjustment was planned or used, how outcomes were grouped for such an adjustment, or whether secondary analyses were considered confirmatory or exploratory. No conclusion about multiplicity control can therefore be drawn.

The primary population is identified as the intent-to-treat population, defined in the record as all randomized patients. That is useful information about the intended analysis population, but it does not establish how participants with missing Month 12 BCVA data were treated. The record does not report the number with missing outcome data, reasons for missingness, imputation methods, or sensitivity analyses. It also does not describe how any deviations from assigned treatment were handled.

Details of the statistical model, covariate adjustment, test procedure, and any interim analyses are not reported in the registry record. The record does not provide an analysis plan that would establish which decisions were made in advance. These gaps make it difficult to assess the robustness of the posted primary comparison or to determine how the reported primary result relates to the full set of planned analyses.

As a general point, randomization supports a group comparison by balancing treatment assignment in expectation, but it does not by itself resolve missing data or multiplicity. Those issues require explicit analysis and reporting. The posted summaries should therefore be treated as a limited account of the available outcome evidence rather than a complete statistical analysis record.

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: gangrene (2.4%), pneumonia (1.6%), coronary artery disease (1.6%), neuropathic arthropathy (1.6%), osteoarthritis (1.6%).

The serious adverse event summary reports 23 affected participants among 125 at risk in the dexamethasone-plus-laser group, and 27 affected among 127 at risk in the sham-plus-laser group. These are group-level counts for participants with serious adverse events; they are not counts of all individual serious events, and a participant may have experienced more than one event. The registry does not report deaths in these group summaries.

The listed serious adverse event terms include Gangrene at 2.4%, Pneumonia at 1.6%, Coronary Artery Disease at 1.6%, Neuropathic Arthropathy at 1.6%, Osteoarthritis at 1.6%, and Cardiac Failure Congestive at 1.6%. The registry summary does not attach these listed term percentages to a specific arm in the information, so they should not be interpreted as arm-specific comparisons.

The other-adverse-event summary reports 125 affected participants among 125 at risk in the dexamethasone group and 127 among 127 at risk in the sham group. These counts indicate that all participants represented in the respective at-risk counts were recorded as having an other adverse event. The registry record does not provide a comparative statistical analysis of adverse events or enough detail to infer event severity beyond the separate serious-event classification.

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

The registry results describe a randomized comparison of dexamethasone implant plus laser photocoagulation with sham implant plus laser photocoagulation for diabetic macular edema. For the primary threshold outcome at Month 12, the reported percentages meeting at least 10 letters of BCVA improvement were 27.8% and 23.6%, respectively. The unadjusted risk-difference estimate is 0.042, and its confidence interval includes zero. The unadjusted p-value is 0.449.

These findings describe the observed group summaries and the uncertainty around their comparison. They do not establish that the treatments are equivalent, because an interval that includes no difference can also include nonzero differences. Nor do the summaries establish a definitive difference. The interval and p-value should be read together with the outcome definition, the analysis population, and the reporting gaps.

The primary endpoint represents reaching a particular improvement threshold, not the full pattern of BCVA changes. It does not summarize all secondary outcomes, all possible visual-acuity outcomes, or the timing of retreatment. The registry lists secondary measures, but their results are not reported in the registry record.

The result is also specific to the comparison tested: both groups received laser photocoagulation, while one group received dexamethasone implant and the other a sham implant procedure. It is not a comparison of laser treatment with no treatment. The study was randomized and triple-masked, but further details about the methods are not reported in the registry record.

Overall, the posted primary summaries leave meaningful uncertainty about the comparative effect on the specified binary BCVA endpoint. They should not be interpreted as medical advice or as a complete account of efficacy or safety. The registry record does not supply the missing-data approach, the original statistical plan, or results for the listed secondary outcomes, all of which would be relevant to a fuller assessment.

16. Why This Trial Matters Statistically

This trial illustrates why a percentage difference should not be interpreted without its uncertainty. The primary outcome percentages were 27.8% and 23.6%, but the unadjusted risk-difference interval includes zero and the p-value is 0.449. The point estimate alone gives an incomplete account: it does not show how much uncertainty surrounds the comparison or how many different underlying effects remain compatible with the data.

It also demonstrates the importance of distinguishing a binary threshold endpoint from a continuous measure. At least 10 letters of improvement is a clearly defined event, and the reported percentages tell readers how often that event occurred. However, the endpoint does not retain all information about changes in letter scores. A full interpretation of visual-acuity outcomes would require the other reported measures and their results, which are not available in the registry record.

The trial's comparison is specifically an add-on contrast in which both groups received laser photocoagulation. This matters statistically because the group difference concerns the treatment strategies as assigned, not the isolated effect of laser. The randomized parallel-group design provides a framework for such a comparison, but the registry record lacks details about randomization, missing data, adjustment, and the original analysis plan.

Finally, the sample-size illustrations show how planning depends on the target effect and desired power. Smaller target effects require larger participant counts under the stated assumptions. Those figures are planning exercises based on the observed effect, not a description of the original trial's design or a measure of its observed power. Together, these points show why effect estimates, uncertainty, endpoint definition, design, and reporting completeness must be considered together.

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 gives limited detail about the conduct and analysis of this study. It identifies the trial as randomized and triple-masked, but does not report the randomization procedure, allocation concealment, masking procedures, or the roles of the masked parties. The specific re-treatment criteria are also not described, despite being used to guide additional implant or laser treatments.

The primary outcome is reported as a percentage meeting a threshold of at least 10 letters of BCVA improvement. The record does not report the distribution of individual changes or provide enough information to assess the effect of any missing Month 12 measurements. Missing-data counts, reasons, imputation, and sensitivity analyses are not reported in the registry record.

The registry lists four secondary outcomes, but their results are not reported. It also does not report whether multiplicity was addressed, whether covariates were used, or whether interim analyses were conducted. The original sample-size justification and design assumptions are not reported in the registry record; the available planning illustration is a separate calculation based on the observed effect.

The serious adverse event group summaries provide affected-participant counts, but the record does not report deaths in those summaries. The listed serious adverse event terms are not presented as arm-specific comparisons in the reported information. No comparative safety analysis is reported, and the summaries do not describe the duration of follow-up for safety outcomes.

These limitations concern what can be assessed from the registry record; they do not establish that particular procedures were or were not performed. They constrain interpretation of the posted outcome summaries and leave important questions about analysis, missingness, and safety reporting unresolved.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy of a New Treatment in Combination With Laser for Diabetic Macular Edema — NCT00464685.
• Registry record last updated 2019-04-24; status last verified 2019-04.
• Results first posted 2014-08-04.
• 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 identifies NCT00464685 as a completed phase 2 randomized, triple-masked, parallel-group study sponsored by Allergan. It enrolled participants with diabetic macular edema and compared 700 µg dexamethasone implant plus laser photocoagulation with sham implant plus laser photocoagulation. The listed study start date is 2007-05-01, and the primary completion date is 2010-02-08.

The primary outcome was the percentage with at least 10 letters of BCVA improvement from baseline in the study eye at Month 12, in the intent-to-treat population. The posted percentages were 27.8% and 23.6%. The unadjusted risk-difference estimate was 0.042, with p = 0.449 and a confidence interval spanning zero. Four secondary outcomes are listed, but their results are not reported in the registry record. The record also lacks details on the original design assumptions, missing-data handling, and full analysis plan.