Protein Kinase C (PKC) Inhibitor-Diabetic Retinopathy Phase 3 Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Protein Kinase C (PKC) Inhibitor-Diabetic Retinopathy Phase 3 Study (NCT00604383), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Had Sustained Moderate Visual Loss (SMVL) as Defined as a Visual Acuity Loss of ≥15 Letters Measured Twice During a 6-month Period.

2. Clinical Question

The trial’s central question was whether the percentage meeting this visual-loss definition differed between the ruboxistaurin and placebo groups. The primary outcome concerns a sustained change in visual acuity, rather than any single low score: the record defines it as a decrease of at least 15 letters from baseline in best-corrected ETDRS visual acuity that persisted during the last six months of study participation. It also allows for an early discontinuation to count if a qualifying six-month period ended at the participant’s last visit with visual-acuity assessment.

The record lists other outcomes concerning diabetic macular edema, proliferative diabetic retinopathy, and patient-reported visual function and health status. Those outcomes provide additional perspectives, but they are not substitutes for the primary question. Results are not posted for every outcome named in the record, and the reasons for any differences in outcome-specific participant counts are not reported in the registry record.

3. Trial Design

This was a phase 3, randomized, double-masked, parallel-group, placebo-controlled study. It was listed as completed and enrolled 685 participants. The study concerned people with type 1 or type 2 diabetes mellitus and diabetic retinopathy within the ETDRS level range of 47A to 53E. The registry lists ruboxistaurin and placebo as the interventions and describes the study as multicenter.

The record gives 345 participants for the ruboxistaurin primary-outcome group and 340 for placebo. The primary outcome population is specified as all randomized participants. Its timeframe is baseline through 36 months; the outcome definition focuses on visual acuity during Months 30-36, while also addressing participants who discontinued early. The study summary describes daily 32 mg ruboxistaurin over three years.

Randomization is intended to allocate participants to comparison groups without choosing treatment according to their observed characteristics. Double masking means that the study was described as masked for two parties, but the record does not identify those parties or explain the masking procedures. Parallel-group design means that participants were assigned to one of the groups rather than crossing between study interventions.

The record gives a start date of 2001-03 and primary completion date of 2005-06. It does not report the original sample-size justification, allocation ratio as a protocol specification, randomization method, stratification factors, detailed masking procedures, or the full statistical analysis plan. Those details should not be inferred from the group counts or from the analyses posted for the outcome.

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.

Before assignment: This study consisted of a 36-month treatment phase and a 0 to 6-month extended treatment phase. Completers are those who completed the 36-month treatment phase.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants.

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.

Population: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Had Sustained Moderate Visual Loss (SMVL) as Defined as a Visual Acuity Loss of ≥15 Letters Measured Twice During a 6-month Period, measured over Baseline through 36 months.

The primary endpoint is the percentage of participants who had sustained moderate visual loss (SMVL) from baseline through 36 months. SMVL is defined as a decrease of at least 15 letters from baseline in best-corrected ETDRS visual acuity, sustained during the last six months of study participation, identified as Months 30-36. For participants who discontinued early, the record allows a qualifying six-month period ending at the last visit at which visual acuity was assessed.

The ETDRS chart uses five letters per line, with scores from 0, meaning no letters read correctly, to 100, meaning all letters read correctly. The endpoint therefore translates a change in visual-acuity score into a prespecified event: meeting the threshold and duration criterion. A binary endpoint of this kind makes it possible to compare the proportion experiencing the event in each randomized group.

Such an endpoint is used to focus on sustained loss rather than a transient measurement. That distinction is part of the registry definition; the record does not provide evidence about how well the threshold predicts other outcomes or why this specific definition was selected. The primary result should be interpreted as a group comparison for this defined event, not as a description of every participant’s visual-acuity trajectory.

7. Results Posted in the Registry

• Ruboxistaurin: 5.5% (19/345) versus 9.1% (31/340) on control; risk difference -3.6 percentage points (95% CI -7.5 to 0.3), risk ratio 0.60 (0.35–1.05); unadjusted two-proportion z-test p = 0.069.

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 Participants Who Developed Center Involved or Imminently Threatened Diabetic Macular Edema (DME)

• 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:
  • Ruboxistaurin: 44.4% (110/248) versus 49.0% (122/249) on control; risk difference -4.6 percentage points (95% CI -13.4 to 4.1), risk ratio 0.91 (0.75–1.09); unadjusted two-proportion z-test p = 0.300.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ruboxistaurin and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Experienced the Development of Proliferative Diabetic Retinopathy (PDR)

• 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:
  • Ruboxistaurin: 35.9% (124/345) versus 36.5% (124/340) on control; risk difference -0.5 percentage points (95% CI -7.7 to 6.7), risk ratio 0.99 (0.81–1.20); unadjusted two-proportion z-test p = 0.886.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ruboxistaurin and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline up to 36 Months in the National Eye Institute Visual Function Questionnaire-25 (NEI-VFQ-25)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Ruboxistaurin: mean -3.82 versus -4.10 on control; difference 0.28 (95% CI -2.02 to 2.58), standardized effect d = 0.02; z-test p = 0.811.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ruboxistaurin and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes with posted numerical results, the recalculated comparisons do not form a clear, consistent pattern that independently resolves the primary comparison. The endpoints cover distinct domains: development of diabetic macular edema, proliferative diabetic retinopathy, and change in patient-reported visual function. The posted summaries do not establish that these outcomes measure the same underlying process as sustained visual loss.

The secondary results should be read alongside, not in place of, the primary endpoint. They can provide context about other aspects of the trial, but they do not remove the uncertainty around the primary estimate or explain the difference between the sponsor’s analysis and the unadjusted recalculation. The registry also lists change in SF-36 health status as a secondary outcome, but results for that outcome are not reported in the registry record.

Unadjusted secondary comparisons carry less weight when several outcomes are considered because the chance of finding an apparently notable result can increase as more comparisons are examined. General statistical practice may address this through a prespecified hierarchy or multiplicity adjustment, but the registry does not report whether either was used for these secondary outcomes. These results should therefore be treated as exploratory context rather than as a set of definitive, separate claims.

Participant counts differ across some posted secondary outcomes. The record does not report why those counts differ or how missing outcome data were handled. That limits direct comparisons across endpoints and makes it difficult to determine whether the analyzed participants represent the same set of randomized participants for each measure.

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

• Percentage of Participants Who Developed Center Involved or Imminently Threatened Diabetic Macular Edema (DME)
• Percentage of Participants Who Experienced the Development of Proliferative Diabetic Retinopathy (PDR)
• Change From Baseline up to 36 Months in the National Eye Institute Visual Function Questionnaire-25 (NEI-VFQ-25)
• Change From Baseline up to 36 Months in Mental and Physical Components of the Medical Outcomes Study 36-Item Short Form (SF-36) Health Status Questionnaire

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is this? The primary outcome is binary: each participant either met the registry’s definition of sustained moderate visual loss or did not. The reported group percentages represent the fraction of participants with the event, expressed as percentages. For a binary endpoint, comparing event proportions is one way to describe how frequently the event occurred in each group. The record identifies the primary population as all randomized participants.

What does the risk difference say? A risk difference subtracts one group’s event proportion from the other group’s event proportion, with the comparison direction specified for the contrast. The recalculated estimate is -0.036 for ruboxistaurin relative to placebo. A negative estimate means the observed proportion was lower in the ruboxistaurin group. The interval from -0.075 to 0.003 gives a range of values compatible with the posted summary data under the calculation used. Since that range crosses zero, it does not exclude no difference at the interval’s stated confidence level.

The record also gives a recalculated risk ratio of 0.604, with an interval from 0.348 to 1.048, and an odds ratio of 0.581, with an interval from 0.321 to 1.05. A risk ratio compares the event proportions as a ratio; an odds ratio compares event odds. Ratios of 1 represent no relative difference. Both posted intervals include 1, so neither ratio interval excludes the no-difference value. These measures express the same underlying binary comparison on different scales, and they should not be mistaken for adjusted sponsor estimates.

What does a confidence interval contribute? In general, a confidence interval describes the uncertainty around an estimated effect under a specified method and its assumptions. A narrower interval indicates greater precision than a wider interval on the same scale. An interval is not a range containing a known fixed percentage of individual participant outcomes, and it is not the probability that the true effect lies in the particular interval. The registry does not report a confidence interval for the sponsor’s Cochran-Mantel-Haenszel result.

How do p-values fit in? The unadjusted p-value of 0.069 is recalculated from posted summary statistics. The registry’s reported analysis uses the Cochran-Mantel-Haenszel method and gives p = 0.034. In general, the Cochran-Mantel-Haenszel approach can combine evidence about an association across strata. The registry does not report the strata, the factors defining them, or the full implementation of the test. The two p-values should therefore be kept distinct rather than treated as interchangeable estimates of the same calculation.

A p-value measures compatibility between data and a null model under a particular analysis. It is not an effect size, a measure of clinical importance, or a probability that a treatment has or lacks an effect. Differences between p-values can arise when analyses use different adjustments, populations, methods, or assumptions. Which explanation accounts for this discrepancy is not reported in the registry record. Given the recorded discrepancy, the sponsor’s own analysis takes precedence over the simple unadjusted recalculation.

Why might over-dispersion matter? In general, over-dispersion means that observed variability is greater than a model expects. If a model assumes less variability than the data contain, standard errors can be too small and confidence intervals too narrow, making statistical evidence appear stronger than it is. This concept is relevant to some outcome models, but the primary comparison is a binary-outcome comparison and the registry does not report an over-dispersion assessment. It should not be assumed to explain the difference between the two p-values.

How should the other outcome measures be understood? The posted secondary binary outcomes are also expressed as percentages of participants with an event. The visual-function questionnaire outcome is reported as a mean change with a standard deviation. For a mean difference, zero is the no-difference value; for a ratio, 1 is the no-difference value; for a risk difference or mean difference, zero is the no-difference value. In general, a standard deviation describes variation among participant measurements, while a confidence interval describes uncertainty in an estimated group comparison. The registry does not post results for every outcome listed, including the SF-36 outcome.

What is a planning illustration? The sample-size figures are planning illustrations calculated from observed effects, not the trial’s original design assumptions. The stated illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. For binary and other non-time-to-event outcomes, the figures are participants per arm. The listed 80% and 90% power values are planning targets, not estimates of the trial’s achieved power. The original design assumptions are not reported in the registry record.

All recalculated comparisons are simple, unadjusted re-calculations from the posted summary statistics. They do not reproduce the sponsor’s named analysis, and they do not account for unreported analytic details. The registry does not report enough information to determine whether covariate adjustment, stratification, imputation, or other procedures were used in the sponsor’s analysis.

11. Confidence Intervals and Precision

The primary unadjusted risk-difference estimate is -0.036, and its 95% confidence interval runs from -0.075 to 0.003. The interval includes zero, the value corresponding to no risk difference. Thus the recalculated estimate points toward a lower observed event proportion in the ruboxistaurin group, but its precision is not sufficient to rule out no difference using this interval.

The interval also allows values in the opposite direction from the point estimate. This is an important feature of uncertainty: the estimate is not a precise boundary on the true effect, and the endpoints should not be read as the only possible values. The confidence interval summarizes uncertainty under the calculation’s assumptions and is not a guarantee about the effect in another population or setting.

On relative scales, the recalculated risk ratio is 0.604 with a 95% confidence interval from 0.348 to 1.048; the odds ratio is 0.581 with a 95% confidence interval from 0.321 to 1.05. Both intervals include 1, the no-relative-difference value. These estimates are not the sponsor’s reported effect estimates.

The registry’s reported Cochran-Mantel-Haenszel analysis gives p = 0.034 but does not post an effect estimate or confidence interval for that analysis. A p-value alone does not show the size or precision of an effect. The differing sponsor and recalculated p-values make it especially important not to combine the sponsor’s p-value with the recalculated interval as though they were outputs from one analysis. The reason for the discrepancy is not reported in the registry record.

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 planning figures describe participants per arm for the listed non-time-to-event outcomes. They are not total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect as a starting point and consider planning for the full observed effect, 75% of the observed effect, or 50% of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm indicated by the illustration for a design targeting an 80% chance of detecting the specified effect under its assumptions, if that effect is real. The 90% power column gives the corresponding number for a 90% target. These are prospective design calculations, not descriptions of the number actually enrolled or evidence that the trial achieved a particular power.

Smaller effects are harder to distinguish from random variation, so the planning illustrations require more participants per arm when the target is a smaller fraction of the observed effect. The values are sensitive to the assumptions used, including the assumed effect size and analysis framework. They should be read as conditional planning quantities rather than universal sample-size recommendations.

This is not observed power. The calculations are planning illustrations based on the observed effect, and they do not reconstruct the original design process or explain the sponsor’s analysis.

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 = 0.091; treatment proportion p₁ = 0.055; average p̄ = 0.073.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3682 = 0.7216.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3673 = 0.3091.
4. n = (0.7216 + 0.3091)² / (-0.0361)² = 815.0, rounded up to 816 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 <- 0.0911764705882353                          # control proportion
p1 <- 0.0550724637681159                          # 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(604383)
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 = 816 (80% power), 1,091 (90% power)
 75% of observed effect: n per arm = 1,532 (80% power), 2,051 (90% power)
 50% of observed effect: n per arm = 3,632 (80% power), 4,861 (90% power)
power.prop.test: 815 
Simulated power at n = 816 per arm: 0.805 (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. Analyses Reported by the Sponsor

The registry reports a Cochran-Mantel-Haenszel analysis for the primary comparison with p = 0.034. A separate, simple unadjusted recalculation from the posted group summaries gives p = 0.069 and a risk-difference confidence interval from -0.075 to 0.003. The recalculation is not the same analysis as the sponsor’s reported method.

The record flags a discrepancy. In that situation, the sponsor’s own reported analysis takes precedence over the simple unadjusted recalculation when stating the registry’s inferential result. That does not make the recalculation a substitute for the sponsor analysis: it is useful as a transparent comparison based on the posted summary statistics, but it cannot establish the reason for the differing p-values.

The sponsor’s effect estimate, confidence interval, analysis population beyond the stated primary population, strata, and detailed model or test specifications are not reported in the registry record. Consequently, the reported p-value cannot be paired with the recalculated effect estimate as if both arose from the sponsor’s analysis. The record does not establish whether the difference reflects adjustment or another analytic choice.

15. Multiplicity, Missing Data and Analysis Populations

The registry posts one primary analysis, identified as a Cochran-Mantel-Haenszel analysis, and four secondary outcomes are listed in the record. Results are posted for some, but not all, secondary outcomes. Whether the trial prespecified a hierarchy among the outcomes, adjusted for multiple comparisons, or treated secondary analyses as exploratory is not reported in the registry record.

Multiplicity matters because repeated statistical tests create more opportunities for apparently unusual results even when no underlying differences exist. In general, a prespecified testing strategy can help control this issue, but no such strategy should be assumed from the list of outcomes or from the number of analyses posted. The registry’s reported p-value for the primary analysis should not be taken as evidence that the secondary tests were protected against multiplicity.

The primary endpoint population is stated to be all randomized participants. The handling of missing primary outcome measurements, the use of imputation, and whether any sensitivity analyses were conducted are not reported in the registry record. The record describes how early discontinuation could qualify for the primary event if a qualifying six-month period ended at the last visit with visual-acuity assessment, but this does not describe every aspect of missing-data handling.

Some secondary outcomes have participant counts that differ from the primary group counts. Reasons for those differences, the missing-data assumptions, and any method used to account for missing observations are not reported in the registry record. SF-36 is listed as a secondary outcome, but its results are not reported. Interim analyses, stopping rules, and alpha-spending procedures are also not reported.

The original statistical analysis plan, sample-size justification, and full details of the sponsor’s analysis are not reported in the registry record. Without those details, the posted results cannot establish whether all analytic decisions followed prespecified procedures or how the sponsor analysis addressed stratification and other potential sources of variation.

16. 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: coronary artery disease (8.8%), cardiac failure congestive (7.2%), pneumonia (4.1%), renal failure acute (4.1%), anaemia (3.8%).

The serious adverse event summary lists 145 affected participants among 345 at risk in the ruboxistaurin group and 157 among 340 at risk in the placebo group. For other adverse events, the summary lists 314 affected participants among 345 at risk in the ruboxistaurin group and 322 among 340 at risk in the placebo group. These are participant counts in the posted safety summary; they do not, on their own, establish that an event was caused by the intervention.

The record lists coronary artery disease at 8.8%, congestive cardiac failure at 7.2%, pneumonia at 4.1%, acute renal failure at 4.1%, anaemia at 3.8%, and myocardial infarction at 3.8% among the top serious adverse event terms. The registry does not provide enough detail in this summary to interpret these terms as comparative causal effects or to establish how terms were selected for display.

Deaths are not reported in the registry record. Further details about event definitions, timing, severity, relatedness, participant overlap across event terms, and statistical comparisons are not reported in the registry record. The counts should therefore be read as descriptive safety information rather than as proof of benefit or harm.

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

The posted primary results describe a lower observed percentage of sustained moderate visual loss in the ruboxistaurin group than in the placebo group. The unadjusted estimate is uncertain: its confidence interval includes zero, and the corresponding unadjusted p-value is 0.069. The registry’s own Cochran-Mantel-Haenszel analysis reports p = 0.034, but the effect estimate and confidence interval for that analysis are not reported. Because the record flags a discrepancy, the sponsor’s analysis takes precedence over the simple recalculation, while the difference between the analyses remains important context.

These results do not establish a treatment effect with a known magnitude. A p-value is not the probability that the intervention is effective, and a confidence interval does not describe the range of outcomes for individual participants. The posted estimates apply to the stated endpoint, population, and study period; they do not answer questions about outcomes that were not measured or about people outside the defined study population.

The primary endpoint is a specific sustained visual-acuity event, not a complete account of vision or overall health. Secondary measures provide additional information but have their own uncertainty, participant counts, and reporting gaps. The registry’s information does not establish how missing data or multiple secondary comparisons were handled.

Statistical interpretation is not medical advice. The results should be understood as a record of group-level observations and analyses, with uncertainty and incomplete analytic detail. They should not be converted into a recommendation for an individual or into a claim that the intervention works or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, its uncertainty, and the analysis method should be read together. The observed group percentages favor a lower event proportion in the ruboxistaurin group, while the simple unadjusted interval includes the no-difference value. The registry’s reported p-value is from a named analysis and differs from the recalculated p-value. Reporting the distinction prevents a single number from obscuring the uncertainty and analytic differences.

The example also shows why outcome definitions matter. Sustained moderate visual loss is defined using both a threshold and a duration, with a special rule for early discontinuation. A reader needs that definition to understand what the reported percentages represent and what they do not capture.

Finally, the registry record illustrates the importance of reporting the analysis plan, sample-size rationale, missing-data handling, multiplicity strategy, and effect estimates with confidence intervals. Those details help readers assess how the primary result was obtained and how secondary findings should be weighed. Where they are not reported, the statistical interpretation must remain correspondingly limited.

19. 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 justification or the assumptions used when the study was designed. The planning illustrations based on observed effects cannot fill that gap. Nor do they provide evidence about the study’s achieved power.

The sponsor’s primary analysis is reported with a p-value but without an effect estimate or confidence interval. The unadjusted recalculation supplies an estimate and interval from posted summaries, but it is not the sponsor’s analysis. The record does not report enough detail to explain the discrepancy, including the strata or other analytic specifications behind the Cochran-Mantel-Haenszel result.

Missing-data methods are not reported. Although the primary population is described as all randomized participants and the endpoint definition addresses early discontinuation, the registry does not explain how unavailable visual-acuity measurements were treated, whether imputation was used, or whether sensitivity analyses were conducted. Some secondary outcomes have different participant counts, and the reasons are not reported.

The record lists four secondary outcomes, but results are not posted for every listed outcome. Multiplicity procedures and the status of the secondary analyses as confirmatory or exploratory are not reported. Safety summaries are descriptive, with no deaths reported in the record and limited detail about event definitions, timing, or relatedness. These gaps constrain interpretation of both efficacy and safety findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Protein Kinase C (PKC) Inhibitor-Diabetic Retinopathy Phase 3 Study — NCT00604383.
• Registry record last updated 2016-10-06; status last verified 2016-08.
• Results first posted 2016-01-28.
• 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.

23. Record Summary

The registry describes a completed, multicenter, randomized, double-masked, parallel, placebo-controlled phase 3 study of ruboxistaurin for participants with type 1 or type 2 diabetes and diabetic retinopathy at ETDRS levels 47A to 53E. It lists 685 enrolled participants and a study period from 2001-03 to primary completion in 2005-06.

The primary endpoint was the percentage with sustained moderate visual loss through 36 months. The posted group percentages were 5.5% for ruboxistaurin and 9.1% for placebo. The registry reports a Cochran-Mantel-Haenszel p-value of 0.034; the simple unadjusted recalculation gives p = 0.069 and a confidence interval for the risk difference that includes zero. The record flags this discrepancy, so the sponsor’s own analysis takes precedence over the recalculation.

Several secondary outcomes and safety counts are posted, but analytic details, missing-data procedures, multiplicity methods, and the original design assumptions are not reported in the registry record.