Mapracorat Ophthalmic Suspension, 3% for the Treatment of Ocular Inflammation and Pain Following Cataract Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Mapracorat Ophthalmic Suspension, 3% for the Treatment of Ocular Inflammation and Pain Following Cataract Surgery (NCT01591161), a randomized phase 3 study. The primary outcome is Percentage of Participants With Complete Resolution of Anterior Chamber (AC) Cells.

2. Clinical Question

The trial’s stated objective was to compare the safety and efficacy of mapracorat ophthalmic suspension, 3%, with its vehicle for postoperative inflammation and pain following cataract surgery. The primary endpoint focuses on inflammation, measured by anterior chamber cells. It is not a direct measure of every aspect of postoperative pain or ocular status. The registry also lists pain and other inflammation outcomes as secondary measures.

The primary comparison is based on the posted counts: 49 of 245 participants in the mapracorat arm and 15 of 124 in the vehicle arm had complete resolution at 8 days. The reported risk difference is 0.079, with a confidence interval from 0.003 to 0.155 and an unadjusted p-value of 0.058. The interval and p-value do not give the same threshold-based reading; the registry record does not report enough analysis detail to explain that difference. These results describe the recorded endpoint and its statistical uncertainty, not every potential benefit or harm of treatment.

3. Trial Design

This was a phase 3, randomized, double-masked, parallel-group trial. The registry reports enrollment of 369 and describes two arms: mapracorat ophthalmic suspension, 3%, and the vehicle of that suspension. The trial status is completed. The registry dates the study start to 2012-07 and primary completion to 2013-06.

Random allocation is intended to distribute participant characteristics across treatment groups by chance, supporting a comparison between assigned groups. Double masking means the registry classifies the study as having masking at two levels, but it does not specify which people were masked or how masking was maintained. A parallel design assigns participants to an arm for the comparison rather than describing a crossover between treatments. Further details of allocation procedures, masking implementation, treatment duration, and follow-up are not reported in the registry record.

The mapracorat arm had 245 participants in the posted primary outcome results; the Vehicle arm had 124. These are the denominators shown for that outcome. The registry enrollment figure is not a substitute for an endpoint-specific analysis population, and the record does not explain the relationship between enrollment and the outcome denominators. The sample-size justification and the original design assumptions are not reported in the registry record.

The primary endpoint was complete resolution of anterior chamber cells at 8 days. The registry also lists secondary outcomes involving resolution of anterior chamber cells at 15 days, Grade 0 pain at 15 days, resolution of anterior chamber flare, combined cells and flare measures, and treatment failures. Numerical arm results are posted for three secondary outcomes; the registry’s outcome list contains additional measures without corresponding numerical results in the posted results. The record does not describe the full analysis population or handling of participants with missing outcome data.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Complete Resolution of Anterior Chamber (AC) Cells, measured over 8 days.

The primary endpoint is the percentage of participants with complete resolution of anterior chamber (AC) cells at 8 days. AC cells are white blood cells in the aqueous assessed during an ophthalmologist’s slit lamp biomicroscopy examination. The registry describes a scale from Grade 0, no cells seen, through higher grades reflecting increasing cell counts; Grade 4 is more than 30 cells. Complete resolution was defined as Grade 0.

This endpoint turns an examination finding into a binary outcome: each participant either met the Grade 0 definition or did not. The posted results therefore give counts of participants meeting the definition, rather than a mean change in a continuous measurement. The endpoint is used to assess postoperative inflammation, one component of the trial’s stated objective. It does not by itself capture pain, other ocular findings, or the full safety profile.

The examination description includes the lids, conjunctiva, limbus, cornea, anterior chamber, vitreous, and lens, without pupil dilation. Although the broader examination covers several structures, the primary outcome is specifically the AC cell grade. The record does not report additional details such as the assessor’s training, reproducibility procedures, or how borderline grades were resolved. Those details would help readers understand how consistently the clinical finding was classified, but they should not be inferred from the endpoint definition alone.

7. Results Posted in the Registry

• Mapracorat: 20.0% (49/245) versus 12.1% (15/124) on control; risk difference 7.9 percentage points (95% CI 0.3 to 15.5), risk ratio 1.65 (0.97–2.83); unadjusted two-proportion z-test p = 0.058.

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 With Complete Resolution of Anterior Chamber (AC) Cells.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Mapracorat: 35.5% (87/245) versus 24.2% (30/124) on control; risk difference 11.3 percentage points (95% CI 1.7 to 20.9), risk ratio 1.47 (1.03–2.09); unadjusted two-proportion z-test p = 0.027.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Mapracorat than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Grade 0 Pain

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Mapracorat: 69.4% (170/245) versus 44.4% (55/124) on control; risk difference 25.0 percentage points (95% CI 14.6 to 35.5), risk ratio 1.56 (1.26–1.94); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Mapracorat than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Complete Resolution of Anterior Chamber (AC) Flare.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Mapracorat: 67.3% (165/245) versus 41.9% (52/124) on control; risk difference 25.4 percentage points (95% CI 14.9 to 35.9), risk ratio 1.61 (1.28–2.01); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Mapracorat than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes with numerical arm results show a consistent direction in the posted comparisons: the mapracorat arm has a higher recorded proportion for each of the three available outcomes than the Vehicle arm. These measures cover complete resolution of AC cells at 15 days, Grade 0 pain at 15 days, and complete resolution of AC flare at 15 days. Their relationship to the primary result is thematic, because they assess postoperative inflammation or pain, but they differ in endpoint, timing, and clinical meaning.

The later AC-cell measure is closely related to the primary endpoint because both use complete resolution of AC cells, but the assessments occur at different time points. The pain outcome addresses a different symptom, and the flare outcome measures another aspect of anterior chamber inflammation. Similar directions across related outcomes can add context to the primary finding, but they do not make the endpoints interchangeable or establish that one outcome explains another.

The registry lists six secondary outcomes, while numerical arm results are present for three. The remaining listed outcomes include complete resolution of AC flare combined with cells, change in combined AC cells and flare, and treatment failures; numerical arm results for those measures are not reported in the registry record in the posted results. The absence of numerical results does not establish what those outcomes would have shown.

Unadjusted secondary results carry less weight for confirmatory conclusions when several outcomes are examined. Repeated testing can increase the chance of an apparently notable result arising by chance across the set, and adjustment or a prespecified hierarchy can address that concern. The registry does not report whether such a plan was used. The unadjusted p-values are therefore descriptive evidence for the individual posted comparisons, not a documented multiplicity-controlled assessment of the full secondary outcome family.

The secondary findings can be read as supportive context for the endpoint pattern, with substantial qualifications. Their estimates depend on the recorded counts, outcome definitions, and analysis populations, and their interpretation is limited by the lack of reported analysis methods and multiplicity handling. They do not replace the primary endpoint or resolve the differing threshold-based readings of its confidence interval and p-value.

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

• Percentage of Participants With Complete Resolution of Anterior Chamber (AC) Cells.
• Percentage of Participants With Grade 0 Pain
• Percentage of Participants With Complete Resolution of Anterior Chamber (AC) Flare.
• Percentage of Participants With Complete Resolution of Anterior Chamber (AC) Cells and Flare.
• Change From Baseline Anterior Chamber (AC) Cells and Flare Combined
• Percentage of Treatment Failures

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are binary: participants either met the outcome definition or did not. For the primary measure, meeting the definition means having Grade 0 AC cells. The arm counts and denominators describe how many participants met that definition among those included in the posted results. A risk difference compares the proportions between arms by subtracting one arm’s proportion from the other. It is expressed on the proportion scale, so zero represents no difference in the proportions.

What does the risk difference communicate?

The primary risk difference is 0.079. It describes the estimated absolute separation between the two arm proportions, rather than a relative comparison. The secondary risk differences are also posted on this scale. The measure is often useful because it retains the outcome’s original proportion scale and can be read as an absolute contrast. Its interpretation still depends on the outcome definition, the participants included, and the quality of the underlying measurements.

The record also supplies relative measures, including risk ratios and odds ratios, with confidence limits. A risk ratio compares the proportions as a ratio; an odds ratio compares the odds of the outcome. These measures answer different questions from a risk difference and can have different numerical magnitudes. The primary interpretation above emphasizes the risk difference because that is the comparison used in the posted summary. The registry does not report an adjusted model or a rationale for prioritizing one effect measure over another.

How should the p-value be read?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The primary unadjusted p-value is 0.058. The registry’s planning assumptions mention a two-sided significance level of 0.05, but the record does not report the original trial’s analysis plan or identify the test used for this comparison. The p-value should therefore be read as a posted unadjusted summary, not as a complete account of the prespecified statistical decision process.

For the primary outcome, the risk-difference confidence interval is 0.003 to 0.155. A confidence interval gives a range of values compatible with the data under the interval procedure and its assumptions. In repeated use of a valid procedure, intervals constructed in this way have a stated coverage property; an individual interval is not a probability distribution over the true effect. The fact that this interval lies above zero does not match a simple threshold reading of the unadjusted p-value at 0.05. Different procedures or analysis details can yield different summaries, but the registry record does not report enough information to determine the explanation in this case.

Why does masking and randomization matter?

Randomization supports a comparison by assigning participants to groups by chance, which can reduce systematic differences in expectation. It does not guarantee identical groups or eliminate uncertainty. Masking may reduce the influence of expectations on care, assessment, or reporting, depending on who is masked and how the process is carried out. The registry classifies the trial as randomized and double-masked, but details about the randomization method, concealment, and masking procedures are not reported in the registry record.

The endpoint is based on an ophthalmologist’s graded examination. As a general statistical matter, outcome classification can affect estimates when measurements are inconsistent or when assessment differs across groups. Masking can be relevant to this concern, but the registry entry does not establish how masking worked in practice or report reliability measures. Thus, design labels inform the reader about the intended structure without replacing operational details.

What do the posted calculations cover?

The arm comparisons are simple unadjusted recalculations from the posted summary statistics. They do not represent reported covariate-adjusted analyses. The registry reports no analyses in its analysis listing, so no model specification, covariate set, stratification, or alternative estimator is available for review. The discrepancy indicator is false; there is no stated conflict between these recalculations and a sponsor analysis in the record.

General statistical methods also depend on the analysis population and the treatment of missing data. A complete-case comparison, for example, can differ from an analysis that handles missing outcomes under an explicit model. That is a general explanation, not a description of what this trial did: the missing-data method and the definition of the analysis population are not reported in the registry record. Without those details, the posted denominators and counts should be interpreted as the summaries recorded, not as evidence of a particular missing-data strategy.

The primary and secondary measures use counts rather than continuous measurements. Dispersion measures such as standard deviations are therefore not relevant to these binary summaries in the same way they would be for a continuous endpoint. The registry does not report a more detailed statistical analysis plan. Readers should distinguish the numerical comparisons that can be described from the inferential procedures and data-handling choices that remain undocumented.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.079, with a confidence interval from 0.003 to 0.155. The width of an interval conveys the range of values compatible with the data under the interval method: a narrower interval generally represents greater precision, while a wider interval represents more uncertainty. The primary interval is entirely above zero, but the unadjusted p-value of 0.058 is above the 0.05 level used in the registry’s planning assumptions. Because the registry does not report the analysis methods for the test and interval, this difference in threshold-based readings cannot be resolved from the record.

Precision is distinct from whether an estimate is statistically distinguishable from a null value under a particular procedure. It is also distinct from clinical importance. The interval describes uncertainty in the estimated risk difference; it does not establish whether the observed separation matters to patients or whether it would persist in another setting. No clinical threshold for interpreting the size of the risk difference is reported.

The secondary risk-difference intervals are 0.017 to 0.209 for complete resolution of AC cells at 15 days, 0.146 to 0.355 for Grade 0 pain, and 0.149 to 0.359 for complete resolution of AC flare. These intervals also communicate uncertainty, and their ranges should be considered alongside the endpoint definitions and the unadjusted nature of the comparisons. The registry does not report multiplicity adjustment, so the intervals and p-values should not be read as if they were a single prespecified test family with documented error control.

Confidence intervals are affected by the amount of information and by the method used to construct them. As a general point, more information can improve precision, while sparse outcomes or variable measurements can leave greater uncertainty. The registry does not report enough methodological detail to assess the interval procedure, missing-data assumptions, or whether any alternative analyses were conducted. Precision should therefore be judged from the posted ranges while recognizing those limits.

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 are participants per arm, not total events. They are planning illustrations computed from the observed effect, not the trial’s own design calculations. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

For the primary endpoint, the planning figures use the observed risk difference as the reference effect. The entries for 100% of that observed effect are 338 participants per arm for 80% power and 452 participants per arm for 90% power. For 75% of the observed effect, the corresponding figures are 571 and 764 participants per arm. For 50% of the observed effect, they are 1,215 and 1,626 participants per arm.

Power is the chance, under a specified design and assumed effect, of detecting an effect using the stated test and significance level. The 80% column describes a planning target with an 80% chance under those assumptions; the 90% column uses a higher target and therefore requires more participants for the listed effect scenarios. Smaller effects are harder to distinguish from random variation and need more participants to reach the same planned power. These are planning calculations, not observed power.

The displayed planning illustration assumes equal allocation, whereas the posted primary outcome denominators differ between the mapracorat and Vehicle arms. That difference is a feature of the recorded outcome counts; it does not change the stated assumptions behind the planning figures. A sample-size illustration based on the observed effect is sensitive to that effect estimate, so it should not be mistaken for evidence that the original study was designed around the same 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 = 0.121; treatment proportion p₁ = 0.200; average p̄ = 0.160.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5191 = 1.0174.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5161 = 0.4343.
4. n = (1.0174 + 0.4343)² / (0.0790)² = 337.4, rounded up to 338 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 <- 0.120967741935484                          # control proportion
p1 <- 0.2                          # 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(1591161)
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 = 338 (80% power), 452 (90% power)
 75% of observed effect: n per arm = 571 (80% power), 764 (90% power)
 50% of observed effect: n per arm = 1,215 (80% power), 1,626 (90% power)
power.prop.test: 337.4 
Simulated power at n = 338 per arm: 0.803 (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

The registry lists multiple secondary outcomes alongside the primary endpoint. When several outcomes are tested, the chance of obtaining at least one apparently unusual result can rise if each test is interpreted separately without adjustment. Statistical approaches to multiplicity can include adjustment of significance thresholds, control of a family-wise error rate, or a prespecified hierarchy that determines which results are confirmatory. These are general options; the registry record does not report whether any such approach was planned or applied.

The available secondary comparisons are described as unadjusted recalculations, and no reported analyses are listed. Their p-values should not be interpreted as multiplicity-adjusted. The record does not identify a primary testing sequence, distinguish confirmatory from exploratory secondary outcomes, or state which outcomes were included in a prespecified family. Consequently, the secondary p-values are most appropriately treated as individual descriptive summaries rather than as proof that a family of outcomes met a controlled statistical criterion.

Missing data are another important issue for binary outcomes. If outcome status is unavailable for some participants, the analysis may depend on whether those participants are excluded, counted under a particular assumption, or handled through a statistical model. The registry record does not report missing outcome counts, the reason for missingness, or the method used to handle missing data. The posted denominators should not be taken as proof that there were no missing observations.

The analysis populations are also not reported in sufficient detail. The record does not say whether the primary comparison used all randomized participants, participants who received assigned treatment, or a different defined group. It does not report protocol deviations or exclusions from the outcome analyses. These details affect the meaning of a treatment comparison, so the arm counts and denominators should be read as the posted outcome summaries rather than as evidence of a specific analysis population.

Finally, the registry does not report a statistical analysis plan, interim analyses, or the trial’s original sample-size justification. Those omissions prevent assessment of whether the posted comparisons follow prespecified decisions. They do not show that the trial lacked such procedures; they mean only that the procedures are not reported in the registry record.

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

Serious events with the highest arm-level rate: cystoid macular edema (0.4%), colitis (0.4%).

For serious adverse events, the posted figures show 2 affected participants among 245 at risk in the mapracorat group and 0 among 124 at risk in the Vehicle group. The listed serious event terms are Cystoid macular edema at 0.4% and Colitis at 0.4%. The registry does not provide further event-level detail, such as timing, duration, or a reported assessment of relationship to treatment.

The record shows 0 participants affected by other adverse events in each arm in the posted summary. Deaths are not reported in the registry record; the missing death entries should not be interpreted as a confirmed absence of deaths. These figures are counts in the recorded safety summary, not a complete description of every possible safety outcome.

Safety counts are descriptive and require context about observation time, ascertainment, severity, and causality. The record does not report enough detail to determine how those factors were assessed. The serious-event summaries should therefore be read as what was recorded for the trial, not as a stand-alone estimate of comparative safety or a basis for treatment advice.

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

The posted primary results describe complete resolution of AC cells at 8 days in the two trial arms. The estimated risk difference is 0.079, and the confidence interval ranges from 0.003 to 0.155. The unadjusted p-value is 0.058. Together, these values give an estimate and measures of statistical uncertainty, but they do not produce a single uncomplicated threshold-based reading: the interval lies above zero while the p-value exceeds 0.05. The registry record does not report the methods needed to explain this difference.

The results do not by themselves establish the clinical importance of the estimated difference. The registry does not report a threshold for a clinically meaningful change in this endpoint, nor does the primary result measure every relevant aspect of postoperative recovery. Secondary measures offer additional context but have their own definitions and timing, and the registry does not report multiplicity handling or analysis populations.

The trial design labels indicate randomization, double masking, and parallel groups. These features are relevant to how a comparison is structured, but the registry record does not provide enough operational detail to assess allocation concealment, who was masked, or how the masking was maintained. It also does not report the missing-data approach or the original statistical plan. Such information is important when judging how robustly the posted estimates represent the intended comparison.

Safety information is also limited to the recorded adverse-event counts and terms. The record does not provide detail sufficient to assess event timing, causal attribution, or the full safety profile. Therefore, the statistical results should be understood as descriptions of the posted outcomes from this trial, with uncertainty and reporting limitations, rather than as medical advice or a general conclusion about treatment.

17. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, confidence interval, and p-value should be read together rather than reduced to a single label. For the primary outcome, the risk difference is 0.079 and the confidence interval is 0.003 to 0.155, while the unadjusted p-value is 0.058. The interval lies above zero, whereas the p-value is above the 0.05 level used in the stated planning assumptions. The registry record does not document the methods needed to explain this difference. Identifying and retaining that distinction is more informative than forcing the summaries into one threshold-based conclusion.

The record also shows how endpoint construction shapes interpretation. The primary outcome is a binary classification based on Grade 0 AC cells, assessed at 8 days. It is a specific measure of inflammation, not a general measure of all postoperative outcomes. Secondary outcomes extend the clinical picture, but their differing definitions and timing mean they should be interpreted as related, not interchangeable, evidence.

Planning calculations based on observed effects can help illustrate how sample requirements vary with assumed effect size and power target. They do not reveal the original design rationale or the trial’s achieved power. The distinction matters because calculations using an observed effect are not a substitute for a prospective sample-size justification, and estimates from a completed trial are uncertain.

Finally, the registry record makes visible several limits that matter for statistical interpretation: no reported analysis plan, no reported analysis population, no reported missing-data approach, and no reported multiplicity strategy. These omissions do not establish that such procedures were absent. They do constrain how confidently readers can connect the posted comparisons to prespecified inferential claims.

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.

The registry record does not report key eligibility criteria, baseline characteristics, or the full analysis population. As a result, it is difficult to assess how representative the analyzed participants were of the intended postoperative population or whether the posted outcome denominators correspond to all randomized participants. The record also does not describe exclusions, protocol deviations, or missing outcome data.

The primary endpoint depends on grading AC cells during an ophthalmologist’s examination. The record defines the scale and Grade 0 threshold, but does not report assessor training, reliability, adjudication procedures, or masking details. Although the trial is labeled double-masked, the identities of masked parties and the implementation are not reported in the registry record.

Statistical reporting is limited. No analysis results are listed in the registry’s analysis record, and the posted comparisons are unadjusted recalculations. The analysis method for the confidence intervals and p-values is not reported. In particular, the primary risk-difference interval lies above zero while the unadjusted p-value is 0.058; the registry does not explain this differing threshold-based reading.

The record lists six secondary outcomes, but numerical arm results are present for three. It does not report multiplicity handling, a testing hierarchy, or a distinction between confirmatory and exploratory secondary analyses. The original sample-size rationale, interim analyses, and the trial’s statistical plan are also not reported. Safety reporting lacks detail on event timing and attribution, and deaths are not reported in the registry record. These limitations restrict interpretation of the posted results but do not establish that the unreported procedures or information were absent from the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Mapracorat Ophthalmic Suspension, 3% for the Treatment of Ocular Inflammation and Pain Following Cataract Surgery — NCT01591161.
• Registry record last updated 2020-09-03; status last verified 2020-08.
• Results first posted 2020-09-03.
• 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

The registry record identifies NCT01591161 as a completed phase 3, randomized, double-masked, parallel trial of mapracorat ophthalmic suspension, 3%, versus its vehicle following cataract surgery. Enrollment is reported as 369. The primary outcome was complete resolution of AC cells at 8 days, defined as Grade 0 on the stated grading scale.

Complete resolution was recorded for 49 of 245 participants in the mapracorat arm and 15 of 124 in the Vehicle arm. The posted risk difference is 0.079, with a confidence interval of 0.003 to 0.155 and an unadjusted p-value of 0.058. The record does not explain the difference between the interval’s and p-value’s threshold-based readings.

Numerical results are posted for three secondary outcomes, with higher recorded proportions in the mapracorat arm for each. The registry does not report the analysis plan, missing-data approach, analysis populations, or multiplicity strategy. Serious adverse events were recorded for 2 participants in the mapracorat group and 0 in the Vehicle group; deaths are not reported in the registry record.