A Study of the Safety and Efficacy of a New Treatment for Diabetic Macular Edema: 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 Diabetic Macular Edema (NCT00168389), a randomized phase 3 study. The primary outcome is Percentage of Patients With a Best Corrected Visual Acuity (BCVA) Improvement of ≥15 Letters From Baseline in the Study Eye.

2. Clinical Question

The clinical question is framed around a threshold change in visual acuity rather than a comparison of average letter-score changes. A participant counts toward the primary outcome if the study-eye score improves by at least 15 letters from baseline. The registry describes visual acuity as the number of letters read correctly on an eye chart, with higher scores indicating better acuity.

The three-arm design permits comparison of each dexamethasone dose with sham. The posted primary outcome values are 22.1% for Dexamethasone 700 μg, 18.7% for Dexamethasone 350 μg, and 13.3% for Sham. The comparisons are reported against Sham, not as a direct statistical comparison between the two dexamethasone doses. The registry record does not report a direct dose-versus-dose analysis.

This is a question about the observed outcome at the stated endpoint visit, not about how quickly a participant improved or whether improvement persisted after treatment. The registry record lists other visual acuity and retinal thickness outcomes, but their numeric results are not reported in the registry record apart from the secondary ≥10-letter improvement outcome.

3. Trial Design

The study is registered as a phase 3 randomized, quadruple-masked, parallel trial. It enrolled 494 participants and is listed as completed. The registry record gives a start date of 2005-02 and a primary completion date of 2012-06. The sponsor is Allergan. These registry entries describe the trial structure and timing; they do not establish how the study was conducted beyond the stated design classifications and arm descriptions.

Participants were assigned among three groups: Dexamethasone 700 μg, Dexamethasone 350 μg, and Sham. The registry arm descriptions specify injections into the vitreous cavity not less than every 6 months for up to 36 months. The sham procedure is described as a needle-less drug delivery system without study medication, also administered not less than every 6 months for up to 36 months. The registry does not report further details about allocation procedures or which groups of people were included in the masking classification.

The primary outcome is the percentage of patients with an improvement of at least 15 letters in best corrected visual acuity from baseline in the study eye. Its timeframe is Baseline, Month 39/Final Visit. The primary analysis population is described as intent to treat: all randomized patients. The posted arm sizes for this outcome are 163, 166, and 165 for the 700 μg, 350 μg, and Sham groups, respectively. The posted result values are percentages.

The record lists six secondary outcomes, including other visual acuity measures and retinal thickness measured by optical coherence tomography. Numeric results are posted for the ≥10-letter improvement outcome, but numeric results for the other listed secondary outcomes are not reported in the registry record. The registry record does not report the original sample-size justification, the planned statistical analysis methods, interim analyses, or details of missing-data handling.

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 a Best Corrected Visual Acuity (BCVA) Improvement of ≥15 Letters From Baseline in the Study Eye, measured over Baseline, Month 39/Final Visit.

The primary endpoint is the percentage of patients whose best corrected visual acuity in the study eye improved by at least 15 letters from baseline. Best corrected visual acuity, or BCVA, is measured with an eye chart and recorded as the number of letters read correctly. The registry explains that a lower letter score indicates worse visual acuity, while an increase indicates improvement.

Using a threshold turns a continuous letter score into a binary outcome for each participant: the participant either meets the 15-letter improvement threshold or does not. The reported percentage is the proportion of participants meeting that criterion in each group. The registry lists the assessment as occurring at Month 39 or the final visit, and identifies the intent-to-treat population—all randomized patients—as the primary population.

A threshold outcome can be clinically interpretable because it expresses how many participants reached a prespecified level of change, rather than only describing an average change across the group. However, the registry record does not report why the 15-letter threshold was selected or how it was specified in the protocol. The endpoint also does not describe the full distribution of changes: participants just below the threshold and those with no improvement are both outside the event category, while the size of improvement among those who meet the threshold is not distinguished.

The endpoint is specific to the study eye and to the stated assessment visit. It should not be read as a measure of every aspect of vision or as a summary of all outcomes in the trial.

7. Results Posted in the Registry

• Dexamethasone 700 μg: 22.1% (36/163) versus 13.3% (22/165) on control; risk difference 8.8 percentage points (95% CI 0.5 to 17.0), risk ratio 1.66 (1.02–2.69); unadjusted two-proportion z-test p = 0.038.
• Dexamethasone 350 μg: 18.7% (31/166) versus 13.3% (22/165) on control; risk difference 5.3 percentage points (95% CI -2.5 to 13.2), risk ratio 1.40 (0.85–2.31); unadjusted two-proportion z-test p = 0.185.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Patients With a BCVA Improvement of ≥10 Letters From Baseline in the Study Eye

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Dexamethasone 700 μg: 38.7% (63/163) versus 23.0% (38/165) on control; risk difference 15.6 percentage points (95% CI 5.8 to 25.5), risk ratio 1.68 (1.20–2.36); unadjusted two-proportion z-test p = 0.002.
  • Dexamethasone 350 μg: 34.3% (57/166) versus 23.0% (38/165) on control; risk difference 11.3 percentage points (95% CI 1.6 to 21.0), risk ratio 1.49 (1.05–2.11); unadjusted two-proportion z-test p = 0.023.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Dexamethasone 700 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Dexamethasone 350 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists six secondary outcomes, spanning BCVA changes, threshold improvements, retinal thickness measured by optical coherence tomography, and time to a BCVA improvement threshold. Numeric results are posted for the percentage of patients with a ≥10-letter improvement at Month 39 or the final visit. Numeric results for the other listed secondary outcomes are not reported in the registry record.

The available ≥10-letter endpoint has a pattern in the same direction as the primary ≥15-letter endpoint: both dexamethasone groups have higher posted event percentages than Sham. The recalculated unadjusted comparisons for the secondary threshold also have intervals above zero and unadjusted p-values below 0.05. This directional consistency is supportive context, but it does not replace the primary analysis or establish that the secondary outcomes were confirmatory.

Secondary outcomes can help describe different aspects of a trial, such as a less stringent threshold, average score changes, or anatomical measurements. Their interpretation depends on prespecification, measurement, missing data, and the analysis plan. The registry record lists the outcomes but does not report a multiplicity-control strategy or complete numerical findings for the listed set.

When many outcomes or comparisons are examined, the chance of at least one apparently unusual finding can increase. Unadjusted secondary p-values do not account for that accumulation of tests. They should consequently carry less weight than a prespecified primary outcome analyzed according to a documented plan. The original testing hierarchy and any correction for multiple comparisons are not reported in the registry record. The numeric secondary comparison should therefore be treated as an additional descriptive result, not as independent confirmation of the primary finding.

The secondary outcome set also cannot be summarized as uniformly favorable or unfavorable from the available numeric results. Most listed outcomes have no posted numeric summary in the registry record, and the lone reported secondary outcome does not describe the full range of visual acuity or retinal thickness results.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Average Change From Baseline in BCVA in the Study Eye
• Change From Baseline in BCVA in the Study Eye
• Percentage of Patients With a BCVA Improvement of ≥10 Letters From Baseline in the Study Eye
• Average Change From Baseline in Retinal Thickness as Measured by Optical Coherence Tomography (OCT)
• 10th Percentile for Time to BCVA Improvement of ≥15 Letters From Baseline in the Study Eye
• Percentage of Patients With BCVA Improvement of ≥15 Letters From Baseline in the Study Eye at 3-month Intervals

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods determine how trial outcomes are summarized, compared, and interpreted. The registry record identifies the randomized, parallel, masked design and the primary outcome, but does not report the planned statistical analysis methods, the original sample-size justification, interim analyses, or missing-data procedures. The comparisons are recalculated, simple unadjusted comparisons from the posted summary statistics.

What does the binary outcome represent?

The primary endpoint is a binary outcome at the participant level: whether or not a patient had a ≥15-letter improvement in BCVA from baseline at Month 39 or the final visit. The group percentage represents the share meeting this threshold. The outcome is different from average BCVA change, which would use the amount of change in each participant rather than classify participants by whether they reached a cutoff. The registry lists average change and other BCVA measures as secondary outcomes, but their numeric results are not reported in the registry record.

For a binary endpoint, a risk difference compares the event proportions in two groups by subtracting one group proportion from the other. The recalculated risk differences are expressed as proportions: 0.087 for Dexamethasone 700 μg versus Sham and 0.053 for Dexamethasone 350 μg versus Sham. A value above zero indicates a higher observed event proportion in the dexamethasone group than in Sham for the direction used in these comparisons. This is a descriptive interpretation of the estimates, not a treatment recommendation or a conclusion about clinical benefit.

What do the intervals and p-values convey?

A confidence interval is a range of values compatible with the observed data under a specified statistical procedure. It conveys uncertainty about the estimated difference, rather than listing all plausible outcomes for individual patients. A narrower interval indicates greater precision than a wider interval. The registry does not identify the confidence level or calculation method for these intervals, so those details are not reported in the registry record.

A p-value measures how unusual data at least as far from a no-difference reference would be under a statistical model that assumes no difference. The recalculated p-values are unadjusted: they do not account for testing multiple outcomes or contrasts. They are not the probability that the null hypothesis is true, and they do not measure the size or clinical importance of a difference. The p-values for the primary comparisons are 0.038 and 0.185.

Why does randomization matter?

In general, randomization aims to make assigned groups comparable at the point of allocation, including with respect to factors that are measured and factors that are not measured. This supports interpretation of group contrasts as comparisons associated with randomized assignment, subject to issues such as adherence, outcome measurement, and missing data. The registry labels the trial randomized but does not report the allocation sequence method, concealment procedure, or details of implementation. Those specifics are not reported in the registry record.

The intent-to-treat label means the primary population is all randomized patients. In general, analyzing participants according to randomized group preserves the basis of the randomized comparison. The registry record does not explain whether the posted endpoint percentages include all randomized participants, how participants with missing outcomes were handled, or whether any exclusions occurred. Thus the population label is available, while the operational handling of unavailable observations is not.

What does masking contribute?

The trial is classified as quadruple-masked. In general, masking is intended to reduce the influence of knowledge about assignment on participant experience, care, outcome assessment, or analysis, depending on who is masked. The registry record does not specify which parties were masked or whether masking was maintained throughout follow-up. It also does not report an assessment of masking success.

BCVA is based on reading letters on an eye chart, so its measurement follows a stated scoring approach. Even with a defined measure, measurement and assessment procedures can affect observed outcomes. The registry description explains the score direction but does not report assessor training, testing conditions, or quality-control procedures. Those details are not reported in the registry record.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when outcome variability is greater than a model expects. For binary outcomes, a model may assume a particular relationship between the mean event proportion and its variance. If the actual variability is larger, uncertainty estimates based on the simpler assumption can be too small, potentially making intervals too narrow and p-values too low. Whether over-dispersion was assessed or relevant to this trial is not reported in the registry record. The posted recalculations are simple unadjusted comparisons and should not be mistaken for a full model-based analysis.

Several features may affect interpretation beyond the point estimate: the threshold definition, the endpoint timing, the number of participants with available data, and the analysis plan. The trial record specifies the threshold and the Month 39/final-visit timeframe, but does not give the original statistical plan or missing-data methods. That means readers cannot determine from the registry alone whether the reported endpoint was analyzed exactly as initially planned.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated group difference. For the primary outcome, the recalculated risk difference for Dexamethasone 700 μg versus Sham is 0.087, with an interval from 0.005 to 0.170. For Dexamethasone 350 μg versus Sham, the estimate is 0.053, with an interval from -0.025 to 0.132. These are simple unadjusted recalculations from the posted summary statistics.

The first interval is entirely above zero, while the second extends from a value below zero to a value above zero. This indicates that the second comparison is less conclusive about the direction of the difference under the interval calculation used. It does not establish that the groups are identical. The registry record does not state the confidence level or interval method, so the intervals should be described without assigning an unreported confidence level.

The intervals are not especially narrow relative to their estimates, and therefore leave uncertainty about the size of either contrast. In particular, the interval for the 700 μg comparison extends from a value close to zero to a substantially larger positive value; the interval for the 350 μg comparison includes both negative and positive values. The estimates are based on the posted event counts and group sizes, and do not represent adjusted comparisons accounting for covariates or the multiple outcomes.

Precision is also distinct from clinical importance. An interval can describe statistical uncertainty without establishing whether a difference matters to patients or clinicians. The registry record does not report a threshold for a clinically important between-group difference. Nor does it report the original sample-size calculation or its assumptions, so the achieved precision cannot be compared with a stated design target.

These intervals do not account for unknown features of the original analysis or unresolved details such as missing endpoint data. The registry identifies the intent-to-treat population, but does not report the approach used for unavailable outcomes. That limitation affects how fully the precision estimates can be evaluated from the registry record alone.

12. 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 the observed effect, not the trial's own design justification. For these binary outcomes, the figures mean participants per arm. They are not total event counts. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect. The original trial's design assumptions are not reported in the registry record.

The 80% power column gives the approximate participants per arm needed for an illustrative design to have an 80% chance of detecting the specified effect under the calculation assumptions, if that effect and model assumptions are correct. The 90% power column gives the corresponding planning number for a higher chance of detecting that effect. These are planning quantities for hypothetical two-arm comparisons, not descriptions of the enrollment or allocation in the three-arm trial.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the required group size changes when the effect to detect is set smaller than the observed estimate. Smaller effects require more participants to detect reliably under the same assumptions. The illustrated values therefore depend strongly on the assumed effect size; they should not be treated as a forecast of the result of a future study.

This is not observed power. Observed power calculated after a trial from its observed effect does not add information beyond the estimate and its uncertainty. The useful role of these calculations is prospective planning: they show how assumptions about the target effect, error rate, allocation, and power affect approximate sample requirements. The registry record does not report whether the actual trial was designed using these assumptions.

13. 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 = 0.133; treatment proportion p₁ = 0.221; average p̄ = 0.177.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5399 = 1.0581.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5363 = 0.4514.
4. n = (1.0581 + 0.4514)² / (0.0875)² = 297.4, rounded up to 298 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 <- 0.133333333333333                          # control proportion
p1 <- 0.220858895705521                          # 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(168389)
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 = 298 (80% power), 398 (90% power)
 75% of observed effect: n per arm = 504 (80% power), 674 (90% power)
 50% of observed effect: n per arm = 1,074 (80% power), 1,437 (90% power)
power.prop.test: 297.4 
Simulated power at n = 298 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.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical tests are conducted across multiple outcomes, time points, groups, or comparisons. Even if each test uses the same nominal threshold, the chance of at least one apparently notable result can increase as the number of tests grows. A prespecified testing hierarchy or another multiplicity procedure can address this issue, but the registry record does not report whether one was planned or used.

The record lists a primary endpoint and six secondary outcomes, and the design has three arms. The posted primary comparisons are each dexamethasone dose against Sham. The registry record does not report a direct comparison between the two dexamethasone doses, a testing hierarchy, or an adjustment across the two primary contrasts. The recalculated p-values are unadjusted; they should not be interpreted as multiplicity-controlled confirmatory results.

Missing data are another important issue for a binary endpoint. If the outcome is unavailable for some randomized participants, the analysis method determines how those participants contribute to the estimated percentages. The primary population is described as intent to treat—all randomized patients—but the record does not state how missing Month 39/final-visit outcomes were handled, how many were missing, or whether any imputation or sensitivity analysis was used. These details are not reported in the registry record.

The registry also does not report the original statistical analysis plan, interim analyses, the planned sample-size justification, or the exact analysis model. It lists 494 enrolled participants and outcome group sizes, but these registry entries alone do not clarify the reasons for any difference between overall enrollment and endpoint denominators. The registry classifies the design as quadruple-masked, but does not specify which parties were masked or describe how the masking designation was implemented.

Without the original analysis plan and missing-data details, it is not possible to verify from the registry record whether the posted results follow the prespecified analysis or how sensitive they are to alternative assumptions. This is a limitation of the registry reporting, not evidence that a particular analysis was or was not performed.

15. 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: myocardial infarction (3.0%), prostate cancer (2.0%), cerebrovascular accident (1.9%), cardiac failure congestive (1.8%), vitreous haemorrhage (1.8%).

The registry posts serious adverse event counts for participants at risk in each group: 52 of 160 for Dexamethasone 700 μg, 52 of 165 for Dexamethasone 350 μg, and 34 of 164 for Sham. It also posts counts for other adverse events: 153 of 160, 162 of 165, and 124 of 164, respectively. These are group-level counts, not adjusted comparisons. The denominators differ from the primary endpoint group sizes, and the registry record does not explain the denominator differences.

The listed serious adverse event terms include Myocardial Infarction (3.0%), Prostate Cancer (2.0%), Cerebrovascular Accident (1.9%), Cardiac Failure Congestive (1.8%), Vitreous Haemorrhage (1.8%), and Atrioventricular Block Complete (1.2%). The record does not identify these percentages as belonging to a specific arm in the information available, so they should not be interpreted as arm-specific rates. Death counts are not reported in the registry record.

Adverse event summaries describe reported events in the study groups; they do not by themselves establish causation. The registry record does not provide comparative statistical analyses, event timing, severity breakdowns beyond the serious-event classification, or detailed attribution to study treatment. These limitations matter when interpreting counts across groups.

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

The posted primary results describe the percentage of participants who reached a ≥15-letter improvement in study-eye BCVA at Month 39 or the final visit. The observed percentages are higher in each dexamethasone group than in Sham, and the recalculated unadjusted risk-difference intervals differ in whether they include zero. These findings summarize the registry outcome data; they are not, on their own, a complete account of the trial's planned statistical analysis.

The endpoint is a threshold measure at a particular visit. It does not show the average change in letter score, the full distribution of individual changes, the time course of improvement, or what happened after the assessment. A participant who falls short of the 15-letter threshold may still have changed, and the binary summary does not distinguish the size of changes among those who meet it. The registry's secondary outcomes include other ways of measuring vision and retinal thickness, but most do not have numeric results posted.

The comparisons are each against Sham and are unadjusted recalculations. They do not establish a direct difference between the two dexamethasone doses. The registry record does not report the prespecified statistical plan, multiplicity approach, missing-data handling, or sponsor-reported formal analyses. As a result, the estimates should be read with the uncertainty and reporting limitations in mind.

These results do not establish whether the observed differences are clinically important, because the registry does not report a clinical-importance threshold for the between-group contrast. They also do not establish whether the findings generalize to people or settings beyond the participants and procedures described in this trial. The results are not medical advice and do not determine an individual person's care.

The safety counts provide additional descriptive information, but are not causal comparisons and include no posted comparative analysis. Together, the efficacy and safety summaries are pieces of evidence from a completed randomized trial; they do not replace review of the complete trial report and analysis plan.

17. Why This Trial Matters Statistically

This trial illustrates how a randomized, parallel design can compare more than one intervention group with a shared control. It also shows why the primary endpoint definition matters: a percentage crossing a 15-letter threshold answers a different question from an average change in BCVA. The reported result is therefore best understood in relation to its specific threshold, study eye, and Month 39/final-visit assessment.

It is also an example of the distinction between a point estimate and its precision. The two unadjusted risk-difference estimates are positive, but their intervals convey different degrees of uncertainty about the direction of the underlying contrast. Reporting only the arm percentages or only the p-values would omit important context about the range of values compatible with the summaries.

The registry record makes clear that a completed phase 3 trial can still leave important statistical details unreported. The randomized design and intent-to-treat population are identified, yet the original sample-size justification, formal analysis methods, multiplicity strategy, and missing-data procedures are not. Those omissions limit the ability to assess whether the posted comparisons reflect the planned confirmatory analysis.

Finally, planning calculations based on observed effects should not be confused with the trial's original design or with evidence that its sample size was adequate. Illustrations using smaller target effects require larger participant counts under the stated assumptions. This helps show why statistical planning depends on the effect one aims to detect, but does not establish what effect the trial was originally powered to detect.

18. 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 does not report the original sample-size calculation or its assumptions, so the adequacy of the trial's planned enrollment cannot be assessed from the record. It also does not report the planned statistical analysis, multiplicity procedure, or interim analyses. The recalculated unadjusted comparisons therefore cannot be confirmed against a prespecified analysis plan.

Missing-data handling is not reported. Although the primary analysis population is labeled intent to treat, the record does not explain how unavailable Month 39/final-visit measurements were treated, whether any participants were excluded from the posted endpoint summaries, or whether sensitivity analyses were performed. The endpoint group sizes are given, but the registry does not explain their relationship to total enrollment beyond identifying the stated population.

The primary endpoint reduces BCVA change to whether a participant reaches the ≥15-letter threshold. This does not preserve the full range of letter-score changes and does not convey the timing or durability of change. The registry lists several other outcomes, but numeric results are unavailable for most of them. Thus the posted endpoint cannot represent every dimension of vision or retinal status assessed by the trial.

The reported comparisons are unadjusted and use recalculations from posted summary statistics. The registry does not report adjusted analyses, a direct comparison between the two dexamethasone doses, or a multiplicity-controlled interpretation. The confidence-interval level and method are also not stated in the registry record.

For safety, denominators differ from the primary endpoint group sizes, the reason is not reported, and the serious-event terms are not identified by arm in the record details available. These limitations restrict comparative interpretation of the safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of the Safety and Efficacy of a New Treatment for Diabetic Macular Edema — NCT00168389.
• Registry record last updated 2014-08-04; status last verified 2014-07.
• 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.

22. Record Summary

NCT00168389 is a completed randomized phase 3 parallel trial of dexamethasone posterior segment drug delivery systems for diabetic macular edema, with Sham as the comparator. The registry lists quadruple masking and total enrollment of 494. The intervention groups received 700 μg or 350 μg dexamethasone, with injections described as occurring not less than every 6 months for up to 36 months.

The primary outcome was the percentage of patients with a ≥15-letter improvement in study-eye BCVA from baseline at Month 39 or the final visit. Posted arm values were 22.1% for 700 μg, 18.7% for 350 μg, and 13.3% for Sham. The recalculated unadjusted comparisons against Sham have risk differences of 0.087 and 0.053, respectively.

The registry record does not report the original sample-size justification, formal analysis plan, multiplicity strategy, or missing-data handling. Numeric results are also absent for most listed secondary outcomes. Safety counts are descriptive, and further comparative safety analyses are not reported in the registry record.