Efficacy and Safety of IBI-10090 in Ocular Surgery Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of IBI-10090 in Ocular Surgery Patients (NCT01606735), a randomized phase 2 study. The primary outcome is Anterior Chamber Cell Count at Day 8 Post-Treatment.

2. Clinical Question

The registry record describes a study of IBI-10090 for inflammation associated with ocular surgery. Its primary question was whether the proportion of patients with an anterior chamber cell count (ACC) of zero at 8 days post-treatment differed among the dose groups. The outcome description says that the proportion with ACC = 0 would be compared for each dosage group.

This is a comparison of outcome proportions at a specified follow-up time. It is not a comparison of change from baseline: baseline ACC values and change scores are not reported in the registry record. The record also does not provide a separate clinical threshold for what constitutes a meaningful difference among dose groups. Therefore, the central statistical reading is the observed proportion in each arm, accompanied by uncertainty intervals and the unadjusted comparisons against the registry’s designated comparator.

3. Trial Design

This was a randomized, parallel-group Phase 2 study. The official title describes it as multicenter and double-masked; the registry classifies masking as quadruple. Those are the masking details reported in the record, and additional information about who was masked is not reported in the registry record. The listed allocation was randomized. Details of the randomization sequence and allocation concealment are not reported in the registry record.

The registry lists an enrollment of 172 and three dose groups: 342 mcg, 517 mcg, and 697 mcg. The arm descriptions contain no further information. The posted outcome counts show 58 participants in the 342 mcg group, 56 in the 517 mcg group, and 58 in the 697 mcg group. These are arm-specific denominators for the reported outcome; the record does not explain any difference between these counts and the enrollment figure.

The primary completion date is 2013-03, the study start is 2012-04, and the overall status is completed. The sponsor is ICON Bioscience Inc. The registry lists treatment of inflammation after ocular surgery as the study purpose, with the condition described as inflammation associated with cataract surgery.

The primary endpoint was assessed at 8 days post-treatment. The registry record does not report the treatment schedule, the exact timing of assessments relative to surgery, details of concomitant care, or the study’s original sample-size justification. Although the record identifies the study as dose-ranging, it does not report a prespecified dose-response model or a formal trend analysis. No secondary outcome measures are posted. These omissions limit how fully the trial’s operational design and analysis strategy can be reconstructed from the registry record alone.

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 Anterior Chamber Cell Count at Day 8 Post-Treatment, measured over 8 days post-treatment.

The primary endpoint is the percentage of patients with anterior chamber cell count (ACC) clearing at 8 days post-treatment. The outcome description defines the relevant status as an ACC of zero and says the proportion reaching that status would be compared across dosage groups. The posted arm results report 50.0% for 342 mcg, 51.8% for 517 mcg, and 60.3% for 697 mcg.

In general, an endpoint based on a count of cells records a clinical finding, while summarizing the result as a proportion with a count of zero makes it a binary outcome: each assessed participant either meets the stated clearing criterion or does not. A proportion is useful for communicating how often the specified status occurred in each group. It also allows direct comparisons of the probability of that status between groups.

The endpoint is relevant to the stated study focus because the registry describes the trial as evaluating treatment of inflammation associated with ocular surgery and identifies ACC as its primary measure. The record does not provide a detailed rationale for selecting this endpoint, a definition of the assessment procedure, or a threshold for a clinically important between-group difference. It also does not report baseline ACC values, so the posted result should be read as the proportion with ACC = 0 at the stated follow-up, not as a measure of individual change from baseline.

7. Results Posted in the Registry

• 517 mcg: 51.8% (29/56) versus 50.0% (29/58) on control; risk difference 1.8 percentage points (95% CI -16.6 to 20.1), risk ratio 1.04 (0.72–1.49); unadjusted two-proportion z-test p = 0.849.
• 697 mcg: 60.3% (35/58) versus 50.0% (29/58) on control; risk difference 10.3 percentage points (95% CI -7.7 to 28.3), risk ratio 1.21 (0.87–1.68); unadjusted two-proportion z-test p = 0.263.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because each participant either had ACC = 0 at the specified assessment or did not. The registry reports the percentage in each group and a 95% confidence interval for that proportion. The comparison records report risk differences, which express the difference between two group proportions on the proportion scale. The available comparisons use 342 mcg as the reference group.

What does a confidence interval communicate?

In general, a confidence interval describes the uncertainty associated with an estimate under the method used to construct it. A narrower interval indicates greater precision under that method, while a wider interval indicates that a broader range of values remains compatible with the data and calculation. It does not mean that individual outcomes fall within the interval, and it does not assign a probability to the true value after the interval has been calculated.

For the group proportions, the posted 95% confidence intervals are 37.13 to 62.87 for 342 mcg, 38.7 to 64.87 for 517 mcg, and 47.76 to 72.93 for 697 mcg. The comparison intervals are on the risk-difference scale: -0.166 to 0.201 for 517 mcg versus 342 mcg, and -0.077 to 0.283 for 697 mcg versus 342 mcg. Because both comparison intervals cross zero, they include no difference as one value compatible with the estimates, while also allowing for differences in either direction.

How should the risk differences and p-values be read?

In general, a risk difference subtracts one group’s event proportion from another’s. Its sign indicates the direction of the comparison according to the order used, and its magnitude gives the difference on the proportion scale. Here, the posted risk difference is 0.018 for 517 mcg versus 342 mcg and 0.103 for 697 mcg versus 342 mcg. The associated unadjusted p-values are 0.849 and 0.263, respectively. A p-value measures how compatible the observed data are with a specified null model under the test’s assumptions; it is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect.

The record does not report the exact test used for these comparisons or the method used to form the arm-level confidence intervals. The estimates are identified as unadjusted recalculations from posted summary statistics. The registry record does not report covariate adjustment, stratification factors, or an adjusted primary analysis. Consequently, the results should be interpreted as simple group comparisons rather than as estimates adjusted for baseline characteristics or study features.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation is greater than a statistical model expects. It can make standard errors too small if the model’s assumptions are too restrictive, which can in turn make confidence intervals too narrow and tests too optimistic. This concern is especially relevant to count outcomes or clustered observations when the analysis model assumes a particular variance structure. The endpoint posted in this record is a binary proportion, and the registry does not describe a model that accounts for over-dispersion, clustering, or repeated observations. The record therefore does not permit an assessment of whether any such adjustment was needed or used.

What analysis details are unavailable?

The registry record does not report a detailed statistical analysis plan, the statistical test for the primary comparison, an approach to missing outcome data, the analysis population, or a method for multiplicity control. It also does not report subgroup analyses, interim analyses, or a prespecified dose-response test. The existence of three dose groups raises a general issue of how multiple comparisons are handled, but the record does not say whether the study’s original analysis adjusted for multiple testing. No adjustment should be presumed from the posted unadjusted estimates.

The study’s own design assumptions and sample-size justification are not reported in the registry record. Separately, the posted planning illustrations use the observed effect as a starting point and state their own assumptions. They are not evidence about the trial’s original planning or the probability that this completed study would detect an effect. These distinctions matter because planning calculations and analyses of observed results answer different questions.

10. Confidence Intervals and Precision

The arm-level confidence intervals indicate considerable uncertainty about the underlying proportion with ACC = 0 at 8 days post-treatment. The 342 mcg estimate is 50.0%, with a 95% confidence interval from 37.13 to 62.87. For 517 mcg, the estimate is 51.8%, with a 95% confidence interval from 38.7 to 64.87. For 697 mcg, the estimate is 60.3%, with a 95% confidence interval from 47.76 to 72.93. Each interval spans a range of possible proportions rather than identifying a single precise value.

The between-group estimates are also imprecise. For 517 mcg compared with 342 mcg, the risk difference is 0.018 and its 95% confidence interval runs from -0.166 to 0.201. For 697 mcg compared with 342 mcg, the risk difference is 0.103 and its 95% confidence interval runs from -0.077 to 0.283. Both ranges include zero and extend to differences in either direction. Thus, the data do not locate the comparative effect narrowly around the point estimate.

In general, confidence intervals are affected by the amount of information available and by the variability of the outcome. The arm-specific denominators reported for the endpoint are 58, 56, and 58, and the intervals remain broad. The posted record does not provide an interval for a direct comparison between 517 mcg and 697 mcg. Nor does it report a clinical threshold that would help determine which differences within these intervals would matter to patients or researchers. Precision should therefore be judged from the reported ranges, not from the point estimates alone.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations give participants per arm, not total participants across arms and not total events. They show planning for 80% power and planning for 90% power under an assumed two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. These calculations are planning illustrations based on the observed effect, not the study’s original design assumptions; the original sample-size justification is not reported in the registry record.

For the 517 mcg versus 342 mcg comparison, planning for 100% of the observed effect gives 12,302 participants per arm for 80% power and 16,469 participants per arm for 90% power. Planning for 75% of the observed effect gives 21,875 participants per arm for 80% power and 29,283 participants per arm for 90% power. Planning for 50% of the observed effect gives 49,224 participants per arm for 80% power and 65,896 participants per arm for 90% power.

For the 697 mcg versus 342 mcg comparison, planning for 100% of the observed effect gives 362 participants per arm for 80% power and 484 participants per arm for 90% power. Planning for 75% of the observed effect gives 647 participants per arm for 80% power and 866 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,462 participants per arm for 80% power and 1,957 participants per arm for 90% power.

In general, the 80% and 90% columns describe the planned chance of detecting the specified effect under the stated assumptions if that effect is real. The higher target requires more participants per arm. Smaller effects also require more participants per arm to detect with the same target power. These figures are not observed power for the completed trial.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.500; treatment proportion p₁ = 0.518; average p̄ = 0.509.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3857.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7069 = 0.5949.
4. n = (1.3857 + 0.5949)² / (0.0179)² = 12,301.9, rounded up to 12,302 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 <- 0.5                          # control proportion
p1 <- 0.517857142857143                          # 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(1606735)
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 = 12,302 (80% power), 16,469 (90% power)
 75% of observed effect: n per arm = 21,875 (80% power), 29,283 (90% power)
 50% of observed effect: n per arm = 49,224 (80% power), 65,896 (90% power)
power.prop.test: 12301.9 
Simulated power at n = 12,302 per arm: 0.804 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

The study has three dose groups and the posted comparisons use the 342 mcg group as the reference for the 517 mcg and 697 mcg comparisons. Testing more than one comparison raises a general multiplicity issue: when several hypotheses are tested, the chance of at least one apparently positive result can differ from the chance associated with a single test. The registry record does not report whether the original analysis adjusted for multiple comparisons, used a testing hierarchy, or defined another multiplicity strategy. The posted p-values are unadjusted.

The record lists one primary outcome measure and no secondary outcome measures. It also lists zero analysis records. The registry record does not report whether additional analyses were conducted but not posted, whether the stated comparisons were prespecified, or how any subgroup or exploratory analyses were distinguished from confirmatory analyses. The absence of those details means the posted results cannot establish the full scope of analyses planned or performed.

Missing-data methods and analysis populations are also not reported in the registry record. The record does not specify whether the primary analysis used all randomized participants, participants who received treatment, participants with an available day-8 assessment, or another defined group. It does not state how a missing ACC assessment was handled or whether any imputation or sensitivity analysis was used. The arm-specific denominators for the outcome are reported, but the reasons for those denominators and any missing outcomes are not described.

Interim analyses, stopping rules, and any adjustments associated with interim monitoring are not reported in the registry record. Neither the detailed statistical analysis plan nor the study’s original sample-size assumptions are reported. These gaps do not alter the numerical results posted for the endpoint, but they limit assessment of how the statistical decisions were planned and whether the reported comparisons represent the full prespecified analysis.

14. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3.5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: corneal endothelial cell loss (5.2%), corneal edema (3.4%), influenza (1.8%), cervix carcinoma (1.7%), endophthalmitis (1.7%).

The safety record lists serious adverse events affecting 6 participants in the 342 mcg group, 2 in the 517 mcg group, and 3 in the 697 mcg group. It also lists other adverse events affecting 2, 2, and 1 participants in those groups, respectively. The corresponding numbers at risk are 58, 56, and 58 for both categories. These are event counts as posted, not comparisons adjusted for exposure time or other differences among groups.

The registry lists the following top serious adverse event terms and percentages: Corneal endothelial cell loss, 5.2%; Corneal edema, 3.4%; Influenza, 1.8%; Cervix carcinoma, 1.7%; and Endophthalmitis, 1.7%. The record does not give a group breakdown for these terms in the posted list, so they should not be assigned to a particular dose group on the basis of this information.

The figures describe events recorded in the registry and do not establish that the study drug caused them. Death counts are not reported in the registry record. The record also does not provide additional detail on event definitions, follow-up duration for safety, or whether participants could contribute more than one event.

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

The posted results describe how often ACC was zero at 8 days post-treatment in each dose group and the uncertainty around those proportions. The observed percentages were 50.0% for 342 mcg, 51.8% for 517 mcg, and 60.3% for 697 mcg. The unadjusted risk-difference estimates compare the latter groups with the 342 mcg group, and both corresponding confidence intervals include zero.

These findings do not establish that the dose groups are equivalent. The registry record reports no equivalence or non-inferiority margin, and the confidence intervals include a range of possible effects. Nor do the results establish the effect of IBI-10090 compared with no treatment or another treatment: the posted comparison is among the listed dose groups, with 342 mcg designated as the comparison group. The record does not describe OG000 as a placebo or provide a different-treatment comparator.

The results also do not describe change from baseline because baseline ACC measurements are not reported. They concern the specified endpoint at the stated follow-up time. The record does not provide a clinically important difference threshold, so the statistical estimates alone cannot determine whether a particular difference would matter clinically.

In general, randomized comparisons can help assess differences between assigned groups, but interpretation depends on design and analysis details. Here, information about analysis populations, missing data, multiplicity, and the detailed statistical plan is not reported in the registry record. The posted endpoint results should therefore be read as descriptive arm proportions and unadjusted comparisons, with the reported uncertainty, rather than as a complete account of every planned analysis or as medical guidance.

16. Why This Trial Matters Statistically

This trial illustrates how a dose-ranging study can generate several related comparisons from one primary endpoint. Reporting group proportions gives a direct description of the observed outcome, while risk differences put comparisons on an absolute scale. Confidence intervals add information about how precisely those estimates are determined. In this record, the point estimates differ across dose groups, but the comparison intervals are broad and include zero, so the numerical ordering alone does not resolve the uncertainty.

The sample-size illustrations also show why the assumed effect matters. Their planning values change substantially across the stated fractions of the observed effect, and the comparisons have different observed effect estimates. In general, designing a study to detect a smaller effect requires more participants under otherwise similar planning assumptions. The displayed calculations are illustrative rather than a reconstruction of the study’s original design, since its original sample-size justification is not reported in the registry record.

Multiplicity and missing-data reporting are important to interpreting multi-arm trials. The record posts comparisons against the 342 mcg group but does not report an adjustment strategy or analysis populations. Those omissions make it difficult to judge the inferential framework beyond the unadjusted estimates. This is a useful reminder that an endpoint estimate, its confidence interval, and its p-value should be interpreted alongside the analysis plan and data-handling details.

Finally, the posted safety counts should be read as event summaries, not as proof of causation. Clear separation between observed event counts, comparative statistical estimates, and causal conclusions is central to careful interpretation of clinical trial records.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific details unavailable. It does not describe eligibility criteria, baseline characteristics, treatment administration, the assessment procedure for ACC, or the handling of participants who lacked a day-8 assessment. The arm descriptions are blank, and the record does not explain the relationship between the enrollment figure and the denominators reported for the endpoint. These omissions limit assessment of the population represented by the results and the conduct of outcome measurement.

The posted record gives arm proportions and unadjusted comparisons but does not report the exact statistical test, an adjusted analysis, a prespecified dose-response analysis, or a detailed statistical analysis plan. The original sample-size justification is not reported in the registry record. Multiplicity handling, analysis populations, missing-data methods, interim analyses, and stopping rules are also not reported. These are relevant to understanding how the analyses were selected and whether the uncertainty estimates account for design or analysis features.

The primary endpoint is reported at one follow-up time, 8 days post-treatment. The record does not provide longer-term results or secondary outcome measures. It also does not provide a direct comparison between 517 mcg and 697 mcg. For safety, death counts are not reported, and the top serious event terms are not broken down by dose group in the posted list. The registry record does not report enough detail to assess event attribution or exposure-adjusted safety comparisons.

These limitations concern the scope and interpretability of the registry record; they do not replace or revise the posted numerical outcomes.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Efficacy and Safety of IBI-10090 in Ocular Surgery Patients — NCT01606735.
• Registry record last updated 2014-09-22; status last verified 2014-09.
• Results first posted 2014-09-22.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT01606735 is a completed, randomized, parallel-group Phase 2 study of IBI-10090 for inflammation associated with ocular surgery. The official title describes a multicenter, double-masked, dose-ranging study; the registry classifies masking as quadruple. Enrollment is listed as 172, with groups titled 342 mcg, 517 mcg, and 697 mcg.

The primary endpoint was the percentage of patients with ACC clearing, defined in the outcome description as ACC = 0 at 8 days post-treatment. The posted proportions were 50.0%, 51.8%, and 60.3%, respectively. Unadjusted comparisons against the 342 mcg group have risk differences of 0.018 for 517 mcg and 0.103 for 697 mcg; both reported confidence intervals include zero.

The record posts serious and other adverse-event counts but does not report death counts. Analysis populations, missing-data methods, multiplicity handling, and the original sample-size justification are not reported in the registry record.