A Phase 3 Study Evaluating the Efficacy and Safety of OCS-01 Opthalmic Suspension Compared to Vehicle 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 A Phase 3 Study Evaluating the Efficacy and Safety of OCS-01 Opthalmic Suspension Compared to Vehicle for the Treatment of Ocular Inflammation and Pain Following Cataract Surgery (NCT06128369), a randomized phase 3 study. The primary outcome is Absence of Anterior Chamber Cells at Visit 6..

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-masked, vehicle-controlled, parallel-group study of OCS-01 following cataract surgery. The registry record identifies Oculis as the sponsor and reports enrollment of 117 participants. The study status is terminated. The recorded start date is 2023-12-18, and the primary completion date is 2024-05-02. The reason for termination is not reported in the registry record.

Participants in the OCS-01 group were assigned one drop of OCS-01 in the study eye once daily for 14 days, beginning 1-day post-surgery. The comparator group received one drop of vehicle on the same schedule. The registry describes the study as double-masked but does not report who was masked, how masking was maintained, or how treatment allocation was generated or concealed. Those details are not reported in the registry record.

The primary endpoint was assessed on Day 15 and counted participants with absence of anterior chamber cells at Visit 6. The posted arm counts were 67 for OCS-01 and 50 for vehicle. The registry says analyses used the treatment actually received and observed data. That description does not by itself establish that every randomized participant was included in each outcome analysis. The specific analysis populations and participant flow from randomization through outcome assessment are not reported in the registry record.

The registry lists secondary outcomes across visits for anterior chamber cells, ocular pain, flare, and use of rescue medication. The overall rescue-medication outcome has a stated timeframe from first dose until Day 22. The full visit schedule, follow-up procedures, and reasons for the terminated status are 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

Analysis population for the primary outcome, as defined in the registry: Analyses were performed based on the actual treatment received, using observed data.

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: The safety population included all randomized participants who received at least 1 dose of study medication.

6. Primary Endpoint

The registry lists the primary outcome as Absence of Anterior Chamber Cells at Visit 6., measured over Day 15..

The primary endpoint counts participants with absence of anterior chamber cells at Visit 6, with the timeframe identified as Day 15. It is a binary outcome: each participant is counted according to whether the specified absence was recorded. The posted results give counts for both treatment groups, rather than a continuous measurement such as a score or laboratory value.

As a general statistical point, a binary endpoint can make the comparison straightforward to interpret when the clinical question is whether a defined finding is present or absent at a particular assessment. Here, the endpoint concerns an observable sign named in the registry as anterior chamber cells. The registry record does not provide the grading criteria, assessor instructions, or threshold used to determine absence, so those measurement details are not reported in the registry record.

A fixed-visit endpoint also defines when the comparison is made. It does not, on its own, describe how quickly the outcome occurred or what happened between visits. The primary time point is Day 15; separate listed secondary outcomes assess cells, pain, and flare at other visits, as well as rescue-medication use. The primary endpoint therefore represents a specific assessment at a specific point after surgery, not a summary of every aspect of postoperative inflammation or pain.

7. Results Posted in the Registry

• OCS-01: 59.7% (40/67) versus 30.0% (15/50) on control; risk difference 29.7 percentage points (95% CI 12.4 to 47.0), risk ratio 1.99 (1.25–3.17); unadjusted two-proportion z-test p = 0.001.

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.

Use of Rescue Medication Overall.

• 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:
  • OCS-01: 23.9% (16/67) versus 60.0% (30/50) on control; risk difference -36.1 percentage points (95% CI -53.1 to -19.1), risk ratio 0.40 (0.25–0.65); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for OCS-01 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the clinical picture beyond the Day 15 primary assessment. They cover absence of anterior chamber cells, absence of ocular pain, absence of flare, absence of both cells and flare, and use of rescue medication at individual visits and overall. This set includes related but distinct aspects of postoperative inflammation and pain, assessed at several time points.

The detailed posted secondary comparison concerns overall rescue-medication use from first dose until Day 22. Its observed direction is consistent with fewer participants in the OCS-01 group using rescue medication than in the vehicle group. That pattern is directionally compatible with the primary result’s higher observed proportion with absence of anterior chamber cells in the OCS-01 group, but the outcomes measure different things and use different timeframes. Agreement in direction does not make the secondary outcome a confirmation of the primary endpoint.

The registry record lists six secondary outcomes, while detailed comparative results are not present for all of them in the posted outcome information. Results for the other listed visits and measures are not reported in the registry record. The broader outcome list therefore describes what was assessed or intended to be assessed, but it does not establish a complete set of posted results across every endpoint.

As a general statistical point, testing several outcomes or time points increases the chance that at least one unadjusted result will appear notable even when there is no underlying difference. Secondary results are often useful for describing consistency and generating questions, but they usually carry less confirmatory weight when the statistical plan, hierarchy, and multiplicity handling are not reported. The registry provides an unadjusted p-value for the overall rescue-medication comparison; whether secondary analyses were prespecified or adjusted for multiple testing is not reported in the registry record.

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

• Absence of Anterior Chamber Cells at Visits 4 and 5.
• Absence of Ocular Pain at Visits 3, 5, and 6.
• Absence of Flare at Visits 4, 5, and 6.
• Absence of Both Anterior Chamber Cells and Flare at Visits 4, 5, and 6.
• Use of Rescue Medication on or Prior to Each Visit.
• Use of Rescue Medication Overall.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants are counted according to whether absence of anterior chamber cells was recorded at Visit 6 on Day 15. The arm summaries report both the number of participants with the event and the number in each group. The registry’s comparison is expressed as a risk difference, with OCS-01 as the treatment group and vehicle as the comparator.

What does the risk difference describe?

As a general statistical explanation, a risk difference subtracts the event proportion in one group from the event proportion in the other. For the primary endpoint, the posted estimate is 0.297 for OCS-01 minus vehicle. A positive value indicates a higher observed proportion with absence of anterior chamber cells in the OCS-01 group. This measure retains the outcome’s original scale and gives an absolute contrast rather than a relative one. It is tied to the particular event definition and assessment time; it does not generalize automatically to other visits or outcomes.

The two group proportions are 0.597 for OCS-01 and 0.3 for vehicle. The registry also gives a risk ratio and an odds ratio for the primary comparison. In general, a risk ratio compares the event proportions, while an odds ratio compares the event odds. The two relative measures use different denominators and can differ in magnitude. Their interpretation depends on which outcome is designated as the event. In this case, the event is absence of anterior chamber cells, not presence of inflammation or use of rescue medication.

How should the p-value be read?

The primary unadjusted p-value is 0.001. As a general statistical explanation, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is correct, the probability that the observed result is due to chance, or a measure of clinical importance. The registry record does not identify the specific test, its assumptions, or whether the reported p-value was prespecified.

The word unadjusted signals that the displayed p-value is not presented as a multiplicity-adjusted value. The record lists multiple outcomes and visits, so the distinction matters when interpreting results beyond the primary comparison. Whether a testing hierarchy or a correction for multiple comparisons was planned is not reported in the registry record. The p-value should therefore be read as the posted unadjusted comparison, not as evidence that all possible analyses or outcomes were accounted for.

What does the confidence interval add?

The primary risk-difference estimate has a 95% confidence interval from 0.124 to 0.47. In general, a confidence interval communicates statistical uncertainty around an estimate: narrower intervals indicate greater precision, while wider intervals indicate less precision, conditional on the method used. The interval is not a guarantee that the true value lies within its limits, and it is not a range containing 95% of participant outcomes. Under the usual repeated-sampling interpretation, the confidence procedure would produce intervals covering the fixed parameter at the stated rate if its assumptions were met. The method used to calculate this interval is not reported in the registry record.

The interval’s limits are both on the positive side of zero, which is consistent with a positive risk-difference estimate under the interval method. This does not resolve questions about missing observations, the population represented by the analysis, or the clinical meaning of the endpoint. Those issues are separate from the mathematical uncertainty conveyed by the interval.

What does the analysis population description mean?

The registry states that analyses were based on the actual treatment received, using observed data. As a general statistical point, an analysis by treatment received can classify participants according to the intervention they actually received rather than solely according to their original randomized assignment. An observed-data analysis uses available outcome observations; depending on how missing information is handled, the analyzed group may differ from the randomized group. The record does not report whether any participants switched treatment, how many observations were missing, or whether any imputation or sensitivity analyses were used.

Randomization is a design feature intended to support comparability between assigned groups. The analysis description based on treatment received is not enough to determine whether the posted comparison preserves the original randomized assignment. The exact analysis population, exclusions, and handling of deviations from assigned treatment are not reported in the registry record. The posted counts should consequently be interpreted as the analyzed arm counts, not assumed to be a complete intention-to-treat analysis.

Why can dispersion matter in other outcome types?

As a general statistical explanation, dispersion describes variability in measurements. For a binary count outcome, the key posted information is the number with the event and the number assessed in each group. A dispersion estimate is not applicable in the same way as it would be for a continuous measure. In count outcomes with extra variation beyond the assumptions of a basic model, over-dispersion can make standard errors too small if it is ignored and can lead to overconfident intervals or tests. That issue is not identified as part of this binary endpoint’s reported analysis, and no model details are reported in the registry record.

More generally, the choice of statistical model and uncertainty calculation should match the outcome scale and design. The registry record reports a risk difference, relative measures, confidence intervals, and p-values for the primary comparison, but does not identify the estimation procedure, covariate adjustment, or test. The planning illustration uses a normal approximation; that stated assumption applies to the planning estimates and should not be taken as evidence of the method used for the trial’s reported primary analysis.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.297, and its 95% confidence interval extends from 0.124 to 0.47. The interval gives a sense of the uncertainty around the estimated group contrast. Both limits are positive, but the span also shows that the result is not an exact value known without error. The registry does not report the method used to calculate the interval, so its specific assumptions cannot be assessed from the record.

In general, the width of a confidence interval depends on the amount and variability of the data, as well as the method used. The primary comparison includes 67 participants in the OCS-01 group and 50 in the vehicle group. These group sizes and the observed event counts are relevant to precision, but the interval should be interpreted using its posted limits rather than an independently reconstructed uncertainty calculation.

A confidence interval is not a range of individual participant outcomes and does not state the probability that the true effect lies within those particular limits. It describes uncertainty in an estimated group-level contrast under a statistical procedure. It also does not address bias arising from missing data, choices of analysis population, or selective reporting. Those factors require information beyond the interval itself, and relevant analysis details are not reported in the registry record.

The relative estimates have their own confidence intervals and scales. Their limits should not be compared directly with the risk-difference limits as if they measured the same quantity. For interpretation of the primary result, the risk-difference interval is especially useful for understanding the absolute contrast in the proportion with absence of cells; the risk ratio and odds ratio express relative contrasts instead.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations expressed as participants per arm for these binary outcomes, not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are design probabilities for hypothetical repeated studies under the assumed effect and model; they are not probabilities that the present result is true. The planning figures are not observed power.

Rows planning for 100%, 75%, and 50% of the observed effect illustrate how the target effect changes the required sample size. Smaller effects are harder to distinguish from random variation, so they require more participants under the same planning assumptions. The figures should be read as planning illustrations rather than as evidence that the trial was designed with those targets. They also do not establish why the study enrolled the reported number of participants or why it was terminated.

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 = 0.300; treatment proportion p₁ = 0.597; average p̄ = 0.449.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7033 = 1.3785.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6713 = 0.5649.
4. n = (1.3785 + 0.5649)² / (0.2970)² = 42.8, rounded up to 43 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 <- 0.3                          # control proportion
p1 <- 0.597014925373134                          # 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(6128369)
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 = 43 (80% power), 57 (90% power)
 75% of observed effect: n per arm = 76 (80% power), 101 (90% power)
 50% of observed effect: n per arm = 166 (80% power), 222 (90% power)
power.prop.test: 42.8 
Simulated power at n = 43 per arm: 0.805 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and multiple secondary outcomes, including repeated assessments of cells, pain, and flare across visits, as well as rescue-medication outcomes. Considering several endpoints and time points creates a multiplicity issue: the more comparisons examined, the greater the chance of at least one apparently unusual result under a setting where no true differences exist. As a general statistical point, trial protocols may address this using a prespecified primary endpoint, a testing sequence, or adjustments to significance thresholds. The planned approach for this study is not reported in the registry record.

The posted primary p-value is unadjusted, and the secondary rescue-medication p-value is also described as unadjusted in its comparison. No multiplicity adjustment or testing hierarchy is reported. The registry’s count of outcome measures and its list of secondary outcomes do not disclose whether additional outcomes were measured but not posted, or whether analyses were selected after seeing data. These matters cannot be resolved from the record.

The registry says the primary analyses used actual treatment received and observed data. It does not report the number of missing outcome observations, reasons for missingness, imputation, sensitivity analyses, or whether participants who discontinued treatment were followed for outcome assessment. The specific primary analysis population is not reported in the registry record. Consequently, it is not possible to determine from the posted description whether the arm counts include all randomized participants, only participants with observed Day 15 assessments, or another defined group.

These are distinct sources of uncertainty. Multiplicity concerns how many hypotheses or comparisons were evaluated and how their error rates were handled. Missing-data concerns relate to absent observations and the assumptions used to account for them. The analysis-population question concerns which participants contribute to the estimate. The record does not provide enough information to assess these aspects in detail, and none can be inferred from the numerical result alone.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events among the 67 participants at risk in the OCS-01 group and among the 50 participants at risk in the vehicle group. It also reports zero deaths in both groups. These are the posted serious-event and death counts; they should be read with the group sizes and the registry’s reporting scope in mind.

Other adverse events are reported for 6 participants in the OCS-01 group and 5 participants in the vehicle group. The serious-event term list is empty. The registry record does not provide further detail about the types, severity, timing, or relationship to treatment of those other adverse events. The definitions and collection procedures for adverse events are also not reported in the registry record.

As a general statistical point, observing zero serious events in a study does not establish that the underlying risk is zero. Safety summaries depend on the number of participants observed, duration of follow-up, event definitions, and completeness of reporting. The registry’s terminated status and the reason for termination are not explained in the record, so no inference about the reason can be drawn from the safety counts.

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

The primary posted data show a higher observed proportion with absence of anterior chamber cells at Day 15 in the OCS-01 group than in the vehicle group. The estimated risk difference is 0.297, with a 95% confidence interval from 0.124 to 0.47, and the unadjusted p-value is 0.001. These statistics describe the observed comparison and its uncertainty under the methods used; they do not by themselves establish why the groups differed or how the result should guide care.

The finding is specific to one outcome, one visit, and the participants represented in the posted analysis. It does not establish effects on every aspect of inflammation or pain, all visits, longer-term outcomes, or outcomes not reported in the registry. The secondary outcome list includes related measures, but detailed results are not reported for every listed measure. The observed rescue-medication pattern adds context, yet it is a secondary comparison and should not be treated as a substitute for the primary endpoint.

As a general statistical point, statistical evidence and clinical importance are different questions. A small p-value does not indicate whether an effect is large enough to matter to patients, and the risk difference alone does not establish the relevance of the endpoint threshold or the consequences of the finding. The registry record does not report a threshold for clinical importance or a participant-centered interpretation of the observed difference.

The record describes a randomized, double-masked design, but the analysis description is based on treatment actually received and observed data. Details about missingness, analysis populations, protocol adherence, and the reason for termination are not reported in the registry record. Those limitations constrain causal interpretation and assessment of how representative the posted estimates are. The results are statistical observations from the posted trial data, not individualized predictions or medical advice.

17. Why This Trial Matters Statistically

This study offers a clear example of how a binary clinical endpoint can be summarized using both an absolute contrast and relative measures. Absence of anterior chamber cells is counted at a defined visit, allowing the posted event counts and group proportions to be translated into a risk difference, risk ratio, and odds ratio. Each measure answers a related but distinct statistical question, so the choice of scale affects how the result is communicated.

The endpoint also illustrates why timing matters. A Day 15 comparison describes the outcome at that visit; secondary assessments at other visits and measures such as pain, flare, and rescue-medication use address other questions. A reader should not assume that a result at one time point captures the full course of recovery or every dimension of the postoperative experience.

The record provides a confidence interval and an unadjusted p-value, making it possible to discuss both estimated effect and statistical uncertainty. It also leaves important methodological information unreported, including the statistical plan, the missing-data approach, and the reason for termination. This contrast is useful: a numerical result can be precisely quoted while still requiring caution about what the analysis represents.

Finally, the record’s planning illustrations distinguish the sample size needed for different assumed effect sizes from the observed trial results. That distinction helps prevent a common misreading: planning calculations are not a retrospective measure of how likely the study was to find its observed result. Taken together, the trial is a practical case for reading outcome definitions, analysis populations, uncertainty intervals, multiplicity, and planning assumptions as separate parts of statistical interpretation.

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 reports a terminated study but does not state why it was terminated. Without that context, it is not possible to assess whether termination affected enrollment, follow-up, or the availability of outcome results. The record reports enrollment of 117, but does not provide detailed participant flow, baseline characteristics, or the number of participants with observed data at each visit.

The analysis description says actual treatment received and observed data. It does not identify the exact analysis population, whether results were analyzed according to randomized assignment, how treatment deviations were handled, or how missing observations were addressed. These details affect how closely the estimate reflects the randomized comparison and what population it describes.

The statistical methods for the primary estimate, confidence interval, and p-value are not reported in the registry record. Nor are the original sample-size justification, prespecified effect target, interim analyses, covariate adjustments, or multiplicity strategy. The planning illustration has stated assumptions, but it is not the trial’s original design justification. The reason for the difference between the displayed arm counts is not reported in the registry record.

Measurement details are also limited. The record does not describe the criteria for absence of anterior chamber cells, how assessors were trained, or how masking was maintained. Detailed results are not posted for every listed secondary outcome. Adverse-event information is presented as counts, without event descriptions, severity, timing, or relatedness details. These gaps limit evaluation of measurement quality, completeness of outcome reporting, and the broader safety profile.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Phase 3 Study Evaluating the Efficacy and Safety of OCS-01 Opthalmic Suspension Compared to Vehicle for the Treatment of Ocular Inflammation and Pain Following Cataract Surgery — NCT06128369.
• Registry record last updated 2026-07-30; status last verified 2026-07.
• Results first posted 2026-07-30.
• 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 describes NCT06128369, a Phase 3, randomized, double-masked, vehicle-controlled, parallel-group study sponsored by Oculis. The study evaluated OCS-01 against vehicle following cataract surgery and has a status of terminated. Enrollment was 117.

The primary outcome was absence of anterior chamber cells at Visit 6 on Day 15. The posted counts were 40 of 67 for OCS-01 and 15 of 50 for vehicle. The risk difference was 0.297, with a 95% confidence interval from 0.124 to 0.47 and an unadjusted p-value of 0.001. Overall rescue-medication use and adverse-event counts are also reported.

The registry states that analyses used actual treatment received and observed data. The reason for termination, detailed analysis methods, missing-data handling, original sample-size justification, and multiplicity strategy are not reported in the registry record.