Safety and Efficacy of OMS302 in Subjects Undergoing Intraocular Lens Replacement With Phacoemulsification: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of OMS302 in Subjects Undergoing Intraocular Lens Replacement With Phacoemulsification (NCT01454063), a randomized phase 3 study. The primary outcome is Mean Area-under-the-Curve (AUC) Analysis of Change From Baseline in Pupil Diameter (mm) During Surgery.

2. Clinical Question

The primary endpoint follows pupil diameter from the pre-incision baseline through the end of the procedure, defined as cortical clean-up or wound closure. It represents an average change across the surgical interval rather than a single pupil measurement at one time. The clinical question is therefore whether the treatment groups differed in their average intraoperative pupil-diameter change over that interval.

The trial also included postoperative assessments, including ocular pain, photophobia, visual acuity, and ocular inflammation. These outcomes provide additional information about the study’s stated postoperative aims, but the primary comparison is the intraoperative pupil-diameter measure. The registry record does not report eligibility details, a protocol rationale for the selected endpoints, or a prespecified threshold for a clinically important difference.

3. Trial Design

This was a phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Omeros Corporation. The registry lists 405 participants as the enrollment. The study start is recorded as 2011-09, primary completion as 2012-03, and status as completed. Participants undergoing intraocular lens replacement with phacoemulsification were assigned to OMS302 or placebo. Both were diluted in Balanced Salt Solution and used as the irrigation solution during surgery.

The registry describes masking as quadruple. Masking is a design feature intended to limit the influence of treatment knowledge on study conduct or assessment; the specific people covered by the masking designation are not reported in the registry record. The allocation ratio and details of the randomization procedure are also not reported in the registry record.

The primary endpoint analysis included subjects with interpretable video images obtained during the procedure. The reported group sizes for that endpoint were 184 for OMS302 and 180 for placebo. The safety summaries instead list 201 participants at risk in each group. These counts refer to different registry summaries and should not be treated as interchangeable populations. Reasons for differences between the enrollment total and the endpoint-specific counts are not reported in the registry record.

Alongside the primary intraoperative endpoint, the registry lists postoperative measures of pain, photophobia, best corrected visual acuity, and ocular inflammation. It does not report the trial’s original sample-size justification, detailed eligibility criteria, or the full statistical analysis plan. The study’s own planned power assumptions and any planned interim analyses 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.

Randomized

Reasons for not completing this period:

Treated

Analysis population for the primary outcome, as defined in the registry: Subjects with interpretable video images obtained during intraocular lens replacement (ILR) procedure.

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 Mean Area-under-the-Curve (AUC) Analysis of Change From Baseline in Pupil Diameter (mm) During Surgery, measured over from surgery baseline (pre-incision) through surgery end (time of cortical clean-up/wound closure).

The primary endpoint is the mean area-under-the-curve analysis of change from baseline in pupil diameter, measured in millimeters, from surgery baseline to surgery end. Baseline is immediately before surgical incision, and the endpoint interval ends at cortical clean-up or wound closure. The registry describes an assessment at each minute, with the primary summary based on the complete surgical interval.

To form this summary, the analysis first calculates the area under the pupil-diameter trajectory using the trapezoidal rule. It then divides that area by the total surgery time to obtain a time-averaged pupil diameter, and subtracts the baseline pupil diameter. As a result, the endpoint expresses the average change from baseline across the procedure, not the change at a particular minute. Positive values indicate an average diameter above baseline; negative values indicate an average below baseline.

This measure is used to characterize how pupil diameter changes during the operation as a whole. Averaging across the interval can represent the pattern over time more fully than relying on one measurement, although it also compresses a changing trajectory into one summary. The registry does not report a clinically important difference threshold for this measure or a separate endpoint interpretation tied to specific surgical steps.

The primary summary was reported as a mean and standard deviation by treatment arm. The registry’s specified primary population was subjects with interpretable video images from the procedure, so the result directly describes that analysis population rather than necessarily every enrolled participant.

7. Results Posted in the Registry

• OMS302: mean 0.10 versus -0.50 on control; difference 0.60 (95% CI 0.50 to 0.70), standardized effect d = 1.20; 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.

Mean Area-under-the-Curve Analysis of Ocular Pain Visual Analog Scale (VAS) Score Within 12 Hours Postoperatively

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • OMS302: mean 4.10 versus 9.20 on control; difference -5.10 (95% CI -7.20 to -3.00), standardized effect d = -0.47; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OMS302 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Best Corrected Visual Acuity (BVCA) Log Score on Day 1

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • OMS302: mean 0.10 versus 0.10 on control; difference 0.00 (95% CI -0.04 to 0.04), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OMS302 and the control. The interval gives the range of effects that remain compatible with the data.

Ocular Inflammation in Summed Ocular Inflammation Score (SOIS) Grade on Day 1

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • OMS302: mean 2.70 versus 2.90 on control; difference -0.20 (95% CI -0.45 to 0.05), standardized effect d = -0.16; z-test p = 0.111.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OMS302 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different aspects of the postoperative period and use different scales and analysis methods. Across the detailed numerical results, the direction is not uniform in strength or certainty: the ocular-pain comparison is numerically lower for OMS302, the displayed visual-acuity means are the same, and the inflammation comparison is numerically lower but has uncertainty compatible with no mean difference. This pattern adds context to the primary intraoperative result but does not amount to one combined measure of benefit.

The registry also names photophobia assessments and another postoperative pain assessment among its secondary outcomes. Numerical estimates and analysis results for those named measures are not reported in the registry record. Without those results, they cannot be incorporated into a full quantitative account of the secondary outcome pattern.

Secondary outcomes generally carry less confirmatory weight than the designated primary outcome, especially when many outcomes are assessed. In general, the more separate hypotheses tested, the greater the chance that at least one result appears notable by chance if each is judged without accounting for the collection of tests. The registry does not report a multiplicity adjustment or an ordered testing procedure. The posted secondary p-values should therefore be read as outcome-specific results rather than as definitive confirmation across all postoperative measures.

Differences in scales and time frames also limit cross-outcome comparisons. A mean difference in pain units does not have the same interpretation as a log score or an inflammation score. Nor does a secondary result establish the mechanism of the primary result. These endpoints are useful for describing the broader set of outcomes assessed, but they do not replace the primary analysis or resolve the unreported clinical-importance thresholds.

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

• Mean Area-under-the-Curve Analysis of Ocular Pain Visual Analog Scale (VAS) Score Within 12 Hours Postoperatively
• Photophobia at 6 Hours After Surgery (Ocular Pain and Symptoms Numerical Ordinal Scale [Numerical Rating System - NRS] Scores)
• Photophobia at Day 1 After Surgery (Ocular Pain and Symptoms Numerical Ordinal Scale [Numerical Rating System - NRS] Scores)
• Best Corrected Visual Acuity (BVCA) Log Score on Day 1
• Ocular Inflammation in Summed Ocular Inflammation Score (SOIS) Grade on Day 1
• Ocular Pain VAS Score After Day of Surgery - Day 1

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary endpoint summarize?

The endpoint is a continuous measure: the mean area-under-the-curve change from baseline in pupil diameter during surgery. It begins immediately before incision and ends at cortical clean-up or wound closure. The registry describes measurements at each minute and a trapezoidal-rule calculation. In general, the trapezoidal rule approximates the area under a changing series of measurements by joining adjacent observations with straight lines. Dividing the area by the duration produces a time-averaged value; subtracting baseline expresses the result as a change from the starting measurement.

The reported arm summaries are means with standard deviations. A mean describes the arithmetic average in a group. A standard deviation describes the spread of individual observations around that average; it is not a confidence interval and does not by itself describe the precision of the estimated group mean. The primary endpoint group summaries are based on 184 OMS302 subjects and 180 placebo subjects with interpretable video images.

How should the group difference be read?

The unadjusted re-calculation compares the two posted arm means by subtracting the placebo mean from the OMS302 mean. It estimates a mean difference of 0.6 mm. Its 95% confidence interval is from 0.497 to 0.703 mm, and its unadjusted p-value is <0.001. This is a straightforward summary-statistic comparison, not the sponsor’s complete analysis method.

The registry reports the sponsor’s primary analysis as a Cochran-Mantel-Haenszel analysis of mean difference in final values. That analysis estimates 0.577 mm, with a 95% confidence interval from 0.475 to 0.678 mm and p < 0.001. A Cochran-Mantel-Haenszel procedure is a family of methods that can combine information across strata or categories. The registry does not describe the stratification details, so no more specific account of its implementation is warranted. The sponsor’s estimate is the reported trial analysis; the re-calculation is an unadjusted comparison from group summaries.

What does the p-value tell a reader?

In general, a p-value measures how incompatible the observed data are 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 does not measure the probability that the result will replicate. A smaller p-value can reflect a clearer statistical contrast, but it does not establish clinical importance. The registry’s sponsor-reported p-value for the primary endpoint is < 0.001; the unadjusted re-calculation reports p <0.001.

The registry does not report whether the primary p-value was adjusted for any interim looks, the full set of endpoints, or other planned comparisons. The statistical plan and multiplicity strategy are not reported in the registry record. Consequently, the posted p-value should be read as the result reported for that analysis, without assuming an unreported adjustment or a particular testing hierarchy.

Why can different analyses produce different estimates?

Analyses can differ because they use different estimands, data summaries, or modeling procedures. The re-calculation uses the posted group means and standard deviations to make a simple unadjusted mean comparison. The sponsor’s analysis is identified as a Cochran-Mantel-Haenszel analysis of final values. Those methods need not produce exactly the same estimate or uncertainty interval. The registry does not flag a discrepancy between the analyses, and their reported estimates are close, but that does not make the methods identical.

The primary endpoint’s calculation also depends on the observed time course and total surgery time. The registry states how it formed the endpoint but does not report details about handling video segments that could not be interpreted, incomplete trajectories, or missing minute-level observations. These implementation details can affect how an endpoint is derived and which subjects contribute to it; they are not reported in the registry record.

How should secondary analyses be treated?

The secondary endpoints include continuous measures of ocular pain, visual acuity, and inflammation, as well as photophobia and another pain assessment. Their scales and time frames differ, so a mean difference on one measure cannot be directly equated with a mean difference on another. The registry reports different methods across outcomes, including Cochran-Mantel-Haenszel analyses and a Wilcoxon rank-sum test. A rank-sum test compares the ranks of observations and does not necessarily test a difference in means.

In general, testing many outcomes increases the chance of seeing at least one apparently notable result by chance if each is interpreted as a separate confirmatory test. Adjustment procedures or a prespecified hierarchy can address that issue, but the registry does not report a multiplicity strategy. Secondary results therefore provide supporting or exploratory context rather than the same inferential status as the designated primary analysis.

For continuous outcomes, dispersion and precision should also be distinguished. A standard deviation describes variation among observations, while the standard error and confidence interval describe uncertainty in an estimated quantity. The registry’s arm summaries report standard deviations, and the posted comparisons provide uncertainty intervals for some outcomes. Where the sponsor’s reported analysis does not include an interval, the absence should not be filled in by inference from a different method.

11. Confidence Intervals and Precision

A confidence interval describes the precision of an estimated contrast under the assumptions of the analysis. In general, a narrower interval indicates less sampling uncertainty, while a wider interval indicates greater uncertainty. A 95% confidence interval is constructed by a procedure that, under its assumptions and repeated use, would cover the target quantity in 95% of such intervals. It is not a guarantee that the particular interval contains the true value, nor a range of individual participant responses.

For the primary endpoint, the sponsor reports a mean difference of 0.577 mm and a 95% confidence interval from 0.475 to 0.678 mm. The interval lies above zero, which is consistent with the sponsor’s reported p-value of < 0.001 for a difference from zero under that analysis. The simple unadjusted re-calculation estimates 0.6 mm, with a recalculated interval from 0.497 to 0.703 mm. The two intervals arise from different analysis approaches and should not be treated as interchangeable.

The interval gives information about statistical precision, but not about clinical importance. The registry does not state what size of pupil-diameter difference would matter clinically. Precision also depends on the analysis population and assumptions, including the endpoint’s derivation from video measurements over the procedure. The primary analysis uses subjects with interpretable video images; the record does not provide detail about the effect of unavailable or uninterpretable measurements.

Some secondary outcomes have reported confidence intervals, while others do not. An interval that includes zero indicates that the data and analysis do not rule out a zero mean difference at the interval’s stated confidence level. It does not prove equality. Where the registry reports a p-value but no estimate or confidence interval, the magnitude and precision of the contrast cannot be read from that p-value alone. The relevant sponsor-reported intervals and analysis details should be distinguished from simple re-calculations based on arm summaries.

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 illustrations based on the observed effect, not the trial’s original design calculations. For continuous outcomes, the displayed values are participants per arm, not total participants. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 11 participants per arm for 80% power and 15 participants per arm for 90% power. Planning for 75% of the observed effect gives 20 participants per arm for 80% power and 27 participants per arm for 90% power. Planning for 50% of the observed effect gives 44 participants per arm for 80% power and 59 participants per arm for 90% power.

In plain language, 80% power is the probability, under the planning assumptions and a specified true effect, that the test would meet its chosen statistical criterion. The 90% column describes the corresponding planning target at a higher probability of detection. These are prospective planning concepts, not descriptions of what happened in this completed trial. Smaller effects are harder to distinguish from random variation and therefore require more participants under the same assumptions. These figures are not observed power.

The sample-size values should be interpreted as illustrations tied to the observed estimate and stated fractions, not as recommended enrollment targets. A different assumed effect, analysis method, variance, allocation, or significance criterion could lead to different planning requirements. The registry record does not report whether these assumptions were used when designing the trial.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.600; pooled standard deviation σ = 0.501.
2. n = 2 × (1.96 + 0.842)² × 0.501² / 0.600² = 11.0, rounded up to 11 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
delta <- 0.6                      # observed difference in means
sigma <- 0.501318427494797                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1454063)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 11 (80% power), 15 (90% power)
 75% of observed effect: n per arm = 20 (80% power), 27 (90% power)
 50% of observed effect: n per arm = 44 (80% power), 59 (90% power)
power.t.test: 12 
Simulated power at n = 11 per arm: 0.764 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary endpoint using a Cochran-Mantel-Haenszel method, with a mean difference in final values of 0.577 mm. Its 95% confidence interval is from 0.475 to 0.678 mm, and its p-value is < 0.001. This is the trial’s reported inferential analysis and should be distinguished from the simple recalculation using the posted arm means.

The unadjusted re-calculation gives a mean difference of 0.6 mm, a recalculated 95% confidence interval from 0.497 to 0.703 mm, and p <0.001. It uses the arm summaries and does not reproduce all details of the sponsor’s method. The registry does not flag a discrepancy; the estimates are similar but are not identical because the analysis approaches differ.

The sponsor’s reported result takes precedence as the trial’s own analysis. The registry does not provide enough detail about the Cochran-Mantel-Haenszel implementation to reconstruct it fully or to explain every difference in estimation. The re-calculation is best read as a check on the direction and approximate size of the contrast, not as a substitute for the reported analysis or a claim that the analyses are equivalent.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, time points, or comparisons. In general, if each test is assessed using the same threshold without adjustment, the chance of at least one false-positive result across the set can be greater than for a single test. Prespecified hierarchies, adjustment procedures, or a clear distinction between confirmatory and exploratory outcomes can help readers interpret a family of tests.

This study lists a primary intraoperative pupil-diameter endpoint and secondary outcomes involving postoperative pain, photophobia, visual acuity, and ocular inflammation. The registry record does not report a multiplicity adjustment, a testing hierarchy, or whether secondary analyses were intended to be confirmatory. It also does not report the full statistical analysis plan or any interim analyses. The primary p-value can be described as reported, but the record does not establish how the broader set of analyses was handled for multiplicity.

Missing-data methods are another important part of interpretation. The primary population is defined as subjects with interpretable video images. The record does not report the number of enrolled subjects without interpretable images, reasons for unavailable measurements, methods for handling missing observations, or sensitivity analyses addressing missing data. For the secondary outcomes, detailed analysis-population definitions and missing-data procedures are not reported in the registry record.

The registry does identify different numbers of participants in the endpoint and safety summaries. That difference should not be assigned a cause without further documentation. It may reflect different analysis populations or outcome availability, but the reason is not reported in the registry record. The record also does not specify whether the primary analysis was intention-to-treat, per-protocol, or another named approach; the stated interpretable-video population is the available description.

These omissions do not invalidate the posted estimates, but they limit the ability to assess robustness and the role of unavailable data. Readers can interpret the reported results for the populations and methods described, while recognizing that further information about multiplicity and missingness would be needed for a more complete audit of the statistical plan.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: electrocution (0.5%).

The registry lists 201 participants at risk for serious adverse events in each group. It reports 1 participant affected in the OMS302 group and 0 in the placebo group. The record lists electrocution at 0.5% among the top serious adverse-event terms. Death counts are not reported in the registry record.

These summaries should be read as event counts within the registry’s stated safety populations. A count of zero in a group means no serious event was recorded for that summary; it does not establish that the risk is absent. The record does not provide enough detail to characterize event timing, relatedness to treatment, duration, or clinical course, and those details are not reported in the registry record.

The registry also reports other adverse events affecting 156 of 201 participants in the OMS302 group and 154 of 201 in the placebo group. Those counts are separate from the serious-event counts and should not be conflated with them. The posted summary alone does not establish a causal relationship between study treatment and any event, nor does it provide a complete clinical interpretation of safety.

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

The primary result describes a difference between the OMS302 and placebo groups in the average change from baseline in pupil diameter across the surgical interval. The sponsor-reported estimate is positive, its 95% confidence interval lies above zero, and its p-value is < 0.001. The simple unadjusted re-calculation is similar in direction and approximate size. These statistics indicate a clear statistical contrast in the analyzed population under the reported methods.

That finding does not by itself establish how important the difference is in clinical practice. The registry does not report a threshold for a clinically important change, nor does the statistical contrast describe every participant’s response or the minute-by-minute trajectory. The endpoint compresses measurements over surgery into a time-averaged change, and the primary analysis includes subjects with interpretable video images.

The result also does not establish conclusions for every postoperative outcome. The secondary outcomes cover different measures and time frames, and their pattern is mixed in precision and direction. Some named outcomes do not have numerical results reported in the registry record. The registry does not report a multiplicity strategy, detailed missing-data procedures, or the original sample-size justification, so these aspects cannot be used to strengthen or qualify the findings beyond what is recorded.

Nor does the result establish that the findings apply to people or procedures outside the stated study population. The trial concerns subjects undergoing intraocular lens replacement with phacoemulsification, and the registry provides limited detail about eligibility and generalizability. The appropriate statistical reading is therefore specific: a reported group difference in the defined primary measure among the analyzed subjects, with the stated uncertainty, alongside limitations in the registry’s account of design and analysis details.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters. The primary outcome is not a single pupil-diameter reading; it is an average change derived from repeated measurements across the surgery interval. The registry specifies the baseline, endpoint time, and trapezoidal-rule calculation, allowing readers to understand what the reported mean difference represents. That definition is essential for interpreting both the estimate and its units.

It also illustrates the distinction between a sponsor-reported analysis and a transparent re-calculation from arm summaries. The two primary estimates are close, but they come from different methods. Reporting both makes the underlying comparison easier to inspect while preserving the sponsor analysis as the trial’s own inferential result. The registry does not provide enough detail to reproduce every aspect of the sponsor’s procedure, which demonstrates why complete methods reporting is important.

The record further shows why a primary endpoint should be separated from a collection of secondary outcomes. Pain, visual acuity, and inflammation are measured on different scales and at different times, while photophobia is also included among the listed outcomes. Multiple outcome testing and incomplete reporting of the analysis plan make it important to avoid treating every secondary result as an independent confirmation.

Finally, the trial emphasizes that precision, clinical relevance, and population coverage are separate questions. A confidence interval describes statistical uncertainty, but the record does not define a clinically important difference. The primary analysis population is based on interpretable videos, and the reasons for differences among enrollment and analysis counts are not reported. Each of these details affects how confidently readers can move from a numerical contrast to a broader interpretation.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

A key limitation is that the primary endpoint depends on interpretable intraoperative video images. The registry does not report how many subjects lacked interpretable images, why images were unusable, or how missing portions of a measurement trajectory were handled. The reported primary result therefore applies directly to the stated analysis population, while the relation of that population to all enrolled subjects is not fully described.

The registry lists 405 for enrollment, 184 OMS302 and 180 placebo participants for the primary endpoint, and 201 participants at risk in each group for safety summaries. The record does not explain the differences among these counts. Without that explanation, it is not possible to determine from the registry alone how exclusions, missing endpoint data, or different analysis populations affected each result.

The study reports a primary statistical comparison and selected secondary results, but the full statistical analysis plan is not reported in the registry record. Details of randomization, allocation ratio, the sponsor model’s implementation, multiplicity control, missing-data handling, and interim analyses are also not reported. These gaps limit independent reconstruction of the analyses and evaluation of how prespecified decisions shaped the reported results.

The registry does not give a clinically important difference threshold for the pupil-diameter endpoint or the secondary measures. Statistical separation from zero therefore cannot be translated directly into clinical importance. In addition, the primary measure averages changes across the procedure, which can conceal variation in the time course among participants. The secondary outcomes use different scales and time frames, and results for some named outcomes are not numerically reported in the registry record. These limitations call for a focused interpretation of the reported estimates rather than an all-outcome conclusion.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of OMS302 in Subjects Undergoing Intraocular Lens Replacement With Phacoemulsification — NCT01454063.
• Registry record last updated 2014-08-21; status last verified 2014-08.
• Results first posted 2014-08-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT01454063 is a completed phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Omeros Corporation. It enrolled 405 subjects undergoing intraocular lens replacement with phacoemulsification. OMS302 or placebo, each diluted in Balanced Salt Solution, was used as the surgical irrigation solution.

The primary outcome was mean area-under-the-curve change from baseline in pupil diameter during surgery among subjects with interpretable video images. The sponsor reported a mean difference of 0.577 mm, with a 95% confidence interval from 0.475 to 0.678 mm and p < 0.001. A simple unadjusted re-calculation gave a similar direction and size. The registry also reports postoperative secondary outcomes and adverse-event summaries, but does not report several details needed to fully assess multiplicity, missing data, or the original design assumptions.