Efficacy and Safety Assessment of Intracameral Injection of T2380 in Cataract Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Assessment of Intracameral Injection of T2380 in Cataract Surgery (NCT02101359), a randomized phase 3 study. The primary outcome is The Primary Efficacy Variable is Response Based on the Realisation of the Capsulorhexis Without Use of Any Additive Mydriatic Treatment..

2. Clinical Question

The study also assessed safety, but the registry record identifies one outcome measure and does not post secondary efficacy outcomes. The primary endpoint is tied to a specific operative task and the avoidance of additive mydriatic treatment during that task. This makes the question narrower than a general comparison of all aspects of cataract surgery, recovery, or longer-term vision. Those broader outcomes are not reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, parallel-group study sponsored by Laboratoires Thea. The registry lists cataract as the condition, describes the study as completed, and records enrollment of 609. The study started in 2011-06, with primary completion in 2013-01. The masking status is listed as none, so the trial was open-label according to the registry.

The two groups differed in how mydriasis was supported before surgery. Both groups received tetracaine in the eye to be operated on. Participants assigned to T2380 received an intracameral injection of 200 μL of T2380 at the beginning of surgery. Participants in the reference group received topical mydriatic treatments instilled three times before surgery. The registry’s brief summary describes the comparison as T2380 versus topical mydriatics and anaesthetic.

Random allocation can help make treatment groups comparable at the start of a trial, on average, but it does not remove the potential for bias in outcome assessment or care when masking is absent. That concern is relevant to interpretation of an outcome involving a surgical task and a decision about whether additional mydriatic treatment is used. This is a general methodological consideration; the registry does not describe how outcome assessment or treatment decisions were standardized.

The primary efficacy population was a modified intention-to-treat set rather than simply all randomized patients. It included randomized patients with evidence they used the study medication and who met the specified medication-related non-inclusion criterion. Patients were assigned to the group as treated. The arm descriptions and analysis-population definition should therefore be kept distinct from the overall enrollment figure. The registry record does not report a full participant flow or arm-specific reasons for exclusion from the primary analysis.

The registry records one outcome measure, with the primary efficacy endpoint assessed on Day 0. It lists no posted analysis records and no secondary outcomes. Further detail on the original sample-size justification, the trial’s statistical plan, or any interim analyses is not reported in the registry record.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified ITT (mITT) Set: All randomised patients for whom there was evidence they used the study medication, and who satisfied the non-inclusion criterion concerning unauthorized previous and concomitant medications. Patients were assigned to the treatment group as treated.

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: 609 patients have signed the informed consent, but 18 patients were not selected and /or not randomised. 591 patients were randomised (at selection visit).

6. Primary Endpoint

The registry lists the primary outcome as The Primary Efficacy Variable is Response Based on the Realisation of the Capsulorhexis Without Use of Any Additive Mydriatic Treatment., measured over Day 0.

The primary endpoint is the percentage of responders, defined by whether capsulorhexis was realized without use of any additive mydriatic treatment. The assessment was scheduled for Day 0. In practical terms, the endpoint combines successful completion of a specified step of cataract surgery with the absence of additional mydriatic treatment for that step. It is not a measure of every aspect of surgery or of a later clinical outcome.

A binary endpoint records whether each participant met the response definition or did not. Reporting the percentage of responders gives a group-level description that is easy to interpret in relation to the trial question. Comparing the groups addresses whether the observed response proportions differed under the two assigned approaches. The registry also supplies a risk-difference estimate and other comparative measures.

This endpoint is relevant to the stated objective because it directly reflects the intended use of T2380 for mydriasis during the operation and whether additive mydriatic treatment was needed. A task-specific endpoint can answer a focused question, but its meaning depends on how consistently the task and the no-additive-treatment criterion were applied. The registry record does not provide further operational details, such as rules for judging completion or the criteria for administering additional treatment. It also does not report secondary efficacy outcomes that could broaden the clinical interpretation.

7. Results Posted in the Registry

• T2380: 98.9% (265/268) versus 94.7% (266/281) on control; risk difference 4.2 percentage points (95% CI 1.3 to 7.1), risk ratio 1.04 (1.01–1.08); unadjusted two-proportion z-test p = 0.006.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: a participant either met the response definition or did not. The response definition was realization of the capsulorhexis without use of any additive mydriatic treatment. For a binary outcome, a percentage is the proportion of participants classified as responders in the relevant group. This type of summary is useful when the question concerns whether a defined event occurred, rather than the amount of change on a continuous scale.

What does the risk difference describe?

A risk difference is the difference between the event proportions in two groups. Here, the event is being classified as a responder. A positive estimate means the observed response proportion was higher in the T2380 group than in the reference group, given the comparison’s direction. The registry reports a positive risk-difference estimate and an interval around it. The interval represents uncertainty about the estimate under the statistical method used; it is not a range containing a known fixed treatment effect with certainty.

The arm-level percentages and the comparison estimate serve related but distinct purposes. The percentages show the observed response level in each group. A comparative estimate summarizes the contrast between those levels. The registry also supplies participant counts for the comparison, alongside the analysis-group sizes. These counts belong to the reported endpoint analysis and should not be confused with the overall enrollment figure or the separate safety denominators.

Why are ratio measures also reported?

A risk ratio compares the response proportion in one group with the response proportion in the other. A value above one, for the stated direction, indicates a higher observed response proportion in the T2380 group. An odds ratio compares the odds of response between groups rather than comparing the response proportions directly. When an outcome is common, odds and proportions can differ substantially as measures of relative effect. This is why the odds ratio may appear more extreme than the risk ratio even though both describe the same binary endpoint. These are general properties of the measures, not additional trial findings.

Each effect measure has its own scale and interpretation. The risk difference is an absolute contrast, while risk ratios and odds ratios are relative contrasts. Readers should avoid translating one scale into another unless the required data and calculation are available. The registry’s posted estimates are the sponsor’s reported analysis; recalculated measures from rounded arm summaries may not exactly reproduce an analysis based on participant-level data or the sponsor’s method.

What does the p-value tell the reader?

The registry reports an unadjusted p-value of 0.006. In general, a p-value describes how incompatible the observed data, or data more extreme, would be with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, and it is not the probability that the result arose by chance. It also does not quantify clinical importance. The registry does not report a multiplicity adjustment, so the p-value should be understood as unadjusted rather than as a value adjusted for multiple outcome or analysis opportunities.

Randomization supports a comparison between assigned groups, but the registry says the analysis population was modified intention-to-treat and that participants were assigned to treatment as treated. In general, excluding participants after randomization or classifying them by treatment received can weaken the protection randomization provides against confounding. The registry’s population definition is explicit, but the full participant flow and reasons for non-inclusion are not reported in the registry record. The extent of any resulting impact cannot therefore be assessed from this record alone.

Why does dispersion matter for other outcome types?

Dispersion describes variability in measurements. For a binary endpoint, the main information is the responder proportion and its uncertainty; continuous outcomes would require a summary of spread as well as a measure of central tendency. In count data, over-dispersion occurs when variability is greater than a simple model assumes. A model that underestimates variability can produce intervals that are too narrow and tests that appear more decisive than warranted. This is a general statistical point. The registry identifies the primary measure as a percentage of responders and gives no dispersion statistic for it, which is consistent with a binary rather than continuous outcome. No count-outcome model is described in the registry record.

The registry lists no posted analysis records, even though it reports a primary outcome comparison. The details of the original model, covariate adjustment, analysis software, handling of protocol deviations, and missing-outcome strategy are not reported in the registry record. These omissions limit independent reconstruction of the analysis. They do not invalidate the posted result, but they mean the precise analytical pathway cannot be evaluated from the registry record alone.

Finally, statistical significance and precision are related but different concepts. A p-value summarizes evidence against a null model under the analysis assumptions. An interval conveys a range of effect values compatible with the data and method, illustrating the uncertainty in the estimate. Neither replaces consideration of the endpoint’s meaning, the open-label design, the analysis population, or the scope of outcomes actually reported.

10. Confidence Intervals and Precision

Precision concerns how tightly the data locate an effect estimate. The registry reports a confidence interval for the primary risk-difference comparison, as well as intervals for the risk ratio and odds ratio. The exact risk-difference bounds are not repeated in this explanatory text because one reported bound has more than three decimal places. The registry’s risk-difference interval lies on the positive side of zero. For the risk ratio, the reported estimate is 1.045 with limits of 1.013 and 1.077. For the odds ratio, the estimate is 4.981 with limits of 1.425 and 17.41.

An interval is informative in two ways: its location indicates the direction and scale of effects compatible with the analysis, while its width communicates uncertainty. A narrower interval generally indicates greater precision than a wider interval on the same scale and under comparable methods. The odds-ratio interval is comparatively broad around its estimate, so the magnitude on that scale is less tightly specified than a single point estimate might suggest. This does not change the fact that the reported interval is above one.

The registry does not state the confidence level alongside these intervals, so a confidence percentage is not reported. In general, a confidence interval is constructed by a method that, over repeated studies under its assumptions, would cover the target parameter at the method’s stated rate. It is not a guarantee that the true value lies within the particular interval.

Precision also depends on the analysis population and the validity of the statistical assumptions. The reported primary analysis used the modified intention-to-treat set, and the trial was open-label. The registry does not report enough detail about missing observations, outcome assessment, or the calculation method to evaluate all sources of uncertainty. The intervals quantify statistical uncertainty under the reported analysis; they do not account automatically for every possible bias or limitation in trial conduct.

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 figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario considers an effect to detect expressed as a stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding planning number for a higher chance of detection. These are design calculations, not guarantees that a future study will reach a particular conclusion.

For planning at 100% of the observed effect, the listed figures are 275 participants per arm for 80% power and 367 participants per arm for 90% power. For planning at 75% of the observed effect, the figures are 566 and 757 participants per arm. For planning at 50% of the observed effect, they are 1,446 and 1,935 participants per arm. Smaller effects require more participants to distinguish them from random variation under the same assumptions, which explains the rise in the planning figures as the assumed effect becomes smaller.

The sample-size curve represents this same relationship between the effect targeted and the planned number of participants. These calculations are planning illustrations, not observed power. They should not be read as evidence about the probability that the completed trial’s result is correct.

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 = 0.947; treatment proportion p₁ = 0.989; average p̄ = 0.968.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2500 = 0.4900.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2482 = 0.2089.
4. n = (0.4900 + 0.2089)² / (0.0422)² = 274.4, rounded up to 275 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 <- 0.94661921708185                          # control proportion
p1 <- 0.988805970149254                          # 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(2101359)
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 = 275 (80% power), 367 (90% power)
 75% of observed effect: n per arm = 566 (80% power), 757 (90% power)
 50% of observed effect: n per arm = 1,446 (80% power), 1,935 (90% power)
power.prop.test: 274.4 
Simulated power at n = 275 per arm: 0.846 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome measure and reports no secondary outcomes. It lists zero posted analysis records. The primary outcome is therefore the only posted efficacy result described in the registry record. The registry record does not report whether the original protocol included additional outcomes or analyses that were not posted.

Multiplicity arises when several outcomes, time points, subgroups, or analysis choices are tested. If many tests are conducted, the chance of at least one apparently unusual result can increase unless the analysis plan accounts for that multiplicity. This is a general statistical concern, not evidence that the trial conducted unreported tests. Whether the investigators used a hierarchy, adjustment procedure, or other strategy for multiple testing is not reported in the registry record. The posted p-value is unadjusted.

Missing-data handling is also not described. The primary population required evidence of study-medication use and satisfaction of a medication-related non-inclusion criterion, and participants were assigned to groups as treated. The registry does not report the number or reasons for participants excluded from the primary analysis, the number of missing endpoint observations, or any method used to address missing outcomes. The effect of missingness cannot be assessed from the registry record alone.

The analysis population is modified intention-to-treat, not an explicitly reported analysis of every randomized participant according to original allocation. This can matter because post-randomization inclusion criteria may affect comparability between groups. The registry gives the population definition but does not report sensitivity analyses that would show whether conclusions change under alternative inclusion or missing-data assumptions.

Interim analyses and stopping rules are not reported in the registry record. The trial’s complete statistical analysis plan, including any planned covariate adjustment, subgroup analyses, or multiplicity procedure, is also not reported in the registry record. These absences limit assessment of whether the posted analysis followed a prespecified plan; they should not be taken as evidence that such procedures were or were not used.

14. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: macular oedema (0.3%), keratitis (0.3%), cataract operation complication (0.3%), transient ischaemic attack (0.3%), eye haemorrhage (0.3%).

The safety summary reports serious adverse events for 295 participants at risk in the T2380 group and 296 in the reference group. Serious adverse events affected 4 participants in the T2380 group and 6 in the reference group. The registry lists zero other adverse events affecting participants in each group. These are separate safety figures and should not be substituted for the efficacy analysis population sizes.

The registry lists the most frequent serious-event terms as Macular oedema, Keratitis, Cataract operation complication, Transient ischaemic attack, Eye haemorrhage, and Retinal detachment, each reported as 0.3%. These listed terms describe events recorded in the registry; the record does not provide further detail about their timing, severity beyond the serious classification, or relationship to treatment. A term’s listing does not establish that the event was caused by the assigned intervention.

Deaths are not reported in the registry record. Safety counts are descriptive and are not, by themselves, a formal comparison of risk. The registry does not provide inferential estimates or intervals for the serious adverse-event comparison, and the safety results should be interpreted within the reported observation and denominator information.

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

The posted results describe a high response percentage in each group for the specific Day 0 endpoint. The T2380 group had a response rate of 98.9%, and the reference group had a response rate of 94.7%. The registry’s comparative estimate is positive, and the reported unadjusted p-value is 0.006. The confidence intervals for the comparative measures provide additional information about statistical uncertainty, while remaining conditional on the analysis methods and assumptions.

The finding is limited to realization of capsulorhexis without additive mydriatic treatment in the analysis population defined by the registry. It does not answer whether groups differed in other features of surgery, recovery, longer-term outcomes, or patient experience. Those outcomes are not reported as secondary results in the registry record. Nor does the result show that every participant in either group had the same experience: the percentages are group summaries.

Randomization is a strength for comparative inference, but the trial was open-label, and the analysis used a modified intention-to-treat population with participants assigned as treated. These features should be considered when judging how securely the observed contrast can be attributed to the assigned approaches. The registry does not provide enough detail to assess the influence of exclusions, missing endpoint data, or outcome-assessment procedures.

A statistically notable result is not equivalent to proof of clinical importance. The registry does not state a threshold for a difference that would be considered meaningful, and the reported endpoint is focused on one operative step and the use of additive mydriatic treatment. The data therefore support a carefully bounded interpretation: the posted analysis found different response proportions for the defined endpoint, but the record does not establish the implications for outcomes beyond that endpoint or for settings not described by the trial.

The safety summary is also limited. It records serious adverse events and listed event terms, but does not supply a treatment-attribution assessment or a formal comparative safety analysis. These results should be read as reported observations rather than as a complete account of all possible benefits and harms.

16. Why This Trial Matters Statistically

This trial illustrates why the definition of a binary endpoint matters. A response was not simply successful surgery in a broad sense; it required completion of capsulorhexis without additive mydriatic treatment. That definition makes the result interpretable against a specific procedural objective, while also limiting the conclusion to that objective.

It also demonstrates why absolute and relative measures should be read together. The arm percentages communicate the observed response level, the risk difference expresses an absolute contrast, and the risk ratio and odds ratio express relative contrasts on different scales. With a common outcome, those relative measures can look quite different in magnitude. Readers who focus on one ratio alone may misjudge the scale of the observed group difference.

The trial is randomized, but it is not masked. For an outcome tied to an operative task and the use of additional treatment, open-label conduct raises a general question about whether knowledge of group assignment could influence decisions or assessment. Randomization does not automatically resolve that concern. The registry’s limited reporting of analysis details and participant flow further constrains independent appraisal.

Finally, the registry distinguishes the primary efficacy analysis from safety reporting. The primary analysis uses a modified intention-to-treat set; safety denominators are reported separately. Treating those populations as interchangeable, or inferring unreported outcomes from the primary endpoint, would overstate what the record establishes. These features make the study a useful example of reading an effect estimate in context: endpoint definition, scale, precision, population, and design all matter alongside the p-value.

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 reports an open-label design. Because the primary endpoint involves both a surgical task and whether additive mydriatic treatment is used, knowledge of group assignment could be relevant to decisions or assessment. This is a general risk of bias to consider; the registry does not report whether outcome assessors were masked or what procedures were used to standardize decisions.

The primary efficacy result is based on a modified intention-to-treat population defined by study-medication use and a medication-related criterion, with assignment as treated. The registry does not report the full participant flow, arm-specific exclusions, or reasons for missing endpoint data. This limits evaluation of how the analysis population compares with the randomized population and whether exclusions could affect the estimate.

Only one outcome measure is posted, and no secondary outcomes are listed. The endpoint is specific to capsulorhexis without additive mydriatic treatment on Day 0. The registry record does not report broader surgical, recovery, or longer-term efficacy outcomes, so the result cannot be extended to those outcomes from this record alone.

The registry does not report the original sample-size justification, the full statistical analysis plan, any interim analyses, multiplicity procedures, or missing-data methods. The confidence-interval level and the detailed method used to calculate comparative estimates are also not stated. These omissions prevent a complete independent assessment of the analysis choices and their assumptions.

The safety summary provides event counts and selected serious-event terms, but not treatment attribution, detailed event narratives, or formal comparative safety estimates. Deaths are not reported in the registry record. These limitations describe gaps in the registry record; they do not establish that the omitted procedures or information were absent from the study itself.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Efficacy and Safety Assessment of Intracameral Injection of T2380 in Cataract Surgery — NCT02101359.
• Registry record last updated 2014-11-14; status last verified 2014-11.
• Results first posted 2014-09-25.
• 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

NCT02101359 is a completed Phase 3 randomized, open-label, parallel-group trial sponsored by Laboratoires Thea. It enrolled 609 participants and compared intracameral T2380 with a reference approach using topical mydriatics and anaesthetic for cataract surgery. Both groups received tetracaine before surgery.

The primary Day 0 endpoint was response based on realization of capsulorhexis without additive mydriatic treatment. The reported response percentages were 98.9% for T2380 and 94.7% for the reference group; the registry reports an unadjusted p-value of 0.006. The primary analysis used a modified intention-to-treat population.

Safety reporting lists serious adverse events affecting 4 participants in the T2380 group and 6 in the reference group. The registry does not post secondary efficacy outcomes or analysis records. Important details about the original design assumptions, missing data, multiplicity, and the full analysis plan are not reported in the registry record.