Clinical Investigation of the Bacterially-Derived Healon5 Ophthalmic Viscosurgical Device (OVD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Investigation of the Bacterially-Derived Healon5 Ophthalmic Viscosurgical Device (OVD) (NCT02782676), a randomized na study. The primary outcome is Cumulative Rates of Intraocular Pressure (IOP) Spikes 30mm of Mercury (mmHg) or Greater Measured Postoperatively.

2. Clinical Question

3. Trial Design

This was a prospective, multicenter, randomized clinical investigation with a parallel-group model and a paired-eye design. Each subject was to receive investigational Healon5 OVD in one eye and control Healon5 OVD in the fellow eye. The registry lists masking as quadruple. It does not identify the masked roles, so the meaning of that masking designation should not be expanded beyond what is recorded.

The trial compared bacterially-derived Healon5 with the currently available animal-derived Healon5 control. Both interventions are identified as devices. The condition listed is cataract, and the primary outcome timeframe is 3 months. The registry lists the phase as NA. The enrollment entry is 241, while the primary outcome population is described separately as paired-eye subjects in the safety population. That distinction matters: the primary outcome counts are not presented as counts for every enrolled participant.

The record marks the study completed. Its listed start date is 2016-06-21 and its primary completion date is 2017-05-04. The sponsor is Abbott Medical Optics. These record details describe the registered study; they do not establish whether every planned aspect of conduct or analysis was completed as originally intended.

The primary outcome was the cumulative rate of participants with postoperative intraocular pressure spikes of 30 mmHg or greater. Secondary outcomes include ocular serious adverse events, mean change in intraocular pressure from baseline, a rate of pressure spikes of 30 mmHg or greater at 3 months postoperatively, and several grades of inflammation. The record lists 12 outcome measures and 10 posted secondary outcomes. The original statistical plan, including sample-size justification and any planned interim analyses, is not reported in the registry record.

Because treatment was paired between eyes, the design naturally links the two eye-level observations within a subject. The registry does not report enough detail to establish how the statistical analysis accounted for that pairing. That omission is relevant when interpreting the uncertainty around the posted comparison.

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.

Before assignment: 15 subjects are consented but not randomized or treated in the study. 13 subjects were randomized but did not receive study OVD in either eye.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Results are based on paired-eye subjects included in the safety population, which differs from the total number of participant (paired + non-paired eyes)safety population used in the Participant Flow.

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: 208 participants received both products, while 3 only received the Bacterially-Derived OVD and 2 only received the Animal-Derived OVD for a total of 213 paired-eye and non-paired eye subjects.

6. Primary Endpoint

The registry lists the primary outcome as Cumulative Rates of Intraocular Pressure (IOP) Spikes 30mm of Mercury (mmHg) or Greater Measured Postoperatively, measured over 3 months.

The primary endpoint counts participants with at least one postoperative intraocular pressure spike of 30 mmHg or greater during the 3-month timeframe. The registry labels the measure as a cumulative rate, but its posted results are counts: 17 in the investigational-device group and 13 in the control group. Each group has 208 in the endpoint results.

A threshold-based endpoint turns a measured pressure value into an event indicator: a participant either meets the stated threshold or does not. In general, this can make a clinically defined safety event easier to count and compare than a continuous measure alone. It also means the result does not describe the full distribution of pressure values, the size of any pressure increase, or the duration of an elevation. Those are different questions from whether the specified threshold was reached.

The endpoint is relevant to the trial’s stated comparison because the objective was to evaluate non-inferiority for this postoperative event rate. The registry specifies a non-inferiority margin of 10%. A non-inferiority analysis asks whether the data are sufficiently compatible with ruling out an unacceptably worse outcome under a prespecified margin. The registry record does not provide the complete test specification or a formal conclusion, so the counts alone should not be treated as a non-inferiority finding.

The primary population is described as paired-eye subjects included in the safety population. The record notes that this differs from the total participant safety population used in Participant Flow. The endpoint denominator therefore needs to be interpreted according to the outcome-specific population definition.

7. Results Posted in the Registry

• Approved Healon5 OVD (Animal-Derived): 6.2% (13/208) versus 8.2% (17/208) on control; risk difference -1.9 percentage points (95% CI -6.9 to 3.0), risk ratio 0.76 (0.38–1.53); unadjusted two-proportion z-test p = 0.448.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: the measure counts participants with a postoperative pressure spike at or above the stated threshold. A participant either contributes an event or does not for this endpoint. The displayed group results are counts, not averages of pressure values. That distinction matters because a count-based result cannot describe how far pressure values were above or below the threshold.

What does a risk difference describe?

In general, a risk difference compares the event proportions in two groups by subtracting one proportion from the other. It is expressed on the probability scale and is often interpretable as an absolute difference in event frequency. The registry comparison reports a risk difference and a confidence interval, but the estimate is recorded to more decimal places than may be quoted under the display precision limit. The interval is described without reproducing its endpoints: it crosses zero, so the posted interval includes the possibility of no difference. The comparison reports p = 0.448.

The sign and direction of a risk difference depend on which group is subtracted from which. The event counts themselves are unambiguous: 17 events among 208 in the investigational group and 13 among 208 in the approved control group. The comparison labels the control as the comparison arm, but the registry record does not give a plain-language explanation of its subtraction convention. For that reason, the counts are the clearest way to describe which group had the larger posted count.

What does a confidence interval add?

In general, a confidence interval expresses uncertainty around an estimate under a specified statistical procedure. A wider interval signals less precision, while a narrower interval signals greater precision. When an interval for a difference crosses zero, it includes zero difference under that interval’s construction; that is not proof that the groups are the same. The interval also gives a range of estimates compatible with the data and method, rather than a range that guarantees where the true effect lies.

The registry’s comparison includes a confidence interval, but it does not state in the record excerpt whether that interval accounts for the paired-eye structure or how it was constructed. It also does not describe whether the displayed interval is the one used for the primary non-inferiority decision. The interval should therefore be read as the posted comparison’s uncertainty summary, not as a substitute for the full protocol-defined test.

Why does the paired-eye design matter?

General statistical reasoning treats two observations from the same person as potentially related. If one eye receives each device, the outcomes from the two eyes may share characteristics of the same subject. A paired analysis can use the within-subject structure and generally differs from treating every eye as independent. The registry says the study was paired-eye, but the analysis method is not reported in the registry record. No particular paired test or model can be attributed to this trial from the record alone.

The endpoint result is described as being based on paired-eye subjects in the safety population. The record says this differs from the total participant safety population used in Participant Flow. This is a population-definition issue rather than a statistical test: the group used for the endpoint is not described as identical to the general safety population. Reasons for the difference and detailed endpoint missing-data handling are not reported in the registry record.

How should the p-value be read?

In general, a p-value measures how unusual results at least as incompatible with a specified null model would be if that model and the test assumptions held. It does not give the probability that the null hypothesis is true, and it does not measure the probability that a treatment works. The reported p = 0.448 is not evidence of equivalence. A conventional difference test and a non-inferiority test ask different questions: non-inferiority evaluates whether an outcome is no worse than a specified margin, using a suitable estimate and decision rule.

The registry states a 10% non-inferiority margin for the primary endpoint but does not provide a complete test specification, decision result, or detailed statistical analysis plan. The displayed p-value should not be assumed to be the p-value for a non-inferiority test. The registry record also does not report a multiplicity adjustment or a method for handling the paired observations.

Why can event counts be difficult to interpret?

Binary outcomes compress information into event and non-event categories. A threshold event can be important for a safety question, but counts alone do not show event timing, recurrence, duration, or the degree of pressure elevation. The registry’s primary endpoint is cumulative over 3 months; detailed event-time analysis is not reported in the registry record. General statistical interpretation should therefore stay close to the defined endpoint and avoid treating it as a full description of pressure trajectories.

Overall, the posted counts, the displayed comparison, and the stated non-inferiority objective are related but not interchangeable. Counts describe the observed endpoint events. The comparison estimates a difference and reports uncertainty. A non-inferiority conclusion requires the specified margin and an appropriate formal analysis. The registry record reports the first two elements in summary form but does not report the complete analysis needed to verify the third.

10. Confidence Intervals and Precision

The primary comparison is not very precise in the sense that its posted confidence interval crosses zero. That means the interval includes both no difference and differences in either direction under the method used to construct it. The observed event counts are 17 in the investigational group and 13 in the control group, with 208 in each. Those counts indicate the observed ordering, but they do not by themselves determine how uncertain the comparison is.

In general, precision depends on the amount of information in the data, the number of observed events, the variability of the outcome, and the analysis method. Binary outcomes with relatively few events can yield substantial uncertainty, even when group sizes appear similar. In a paired-eye study, the relationship between outcomes from the two eyes can also affect uncertainty. The registry does not report the paired analysis method, so the contribution of that design feature to the posted interval cannot be assessed from the record.

A confidence interval is not a guarantee that the true effect lies within its limits, nor does an interval crossing zero show that the groups are identical. It communicates uncertainty conditional on a statistical model and method. The registry record does not specify enough detail to assess all assumptions behind the posted interval, and it does not state whether that interval is the one used for the non-inferiority decision.

The study’s stated non-inferiority margin is 10%. Interpreting precision against that margin would require a clearly defined effect direction and the relevant confidence bound from the prespecified analysis. The registry provides a posted comparison but does not report the formal non-inferiority conclusion. The data should therefore be read as an uncertain estimate of a difference in this endpoint population, rather than as proof of similarity or non-inferiority.

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 illustrations based on the observed effect, not the trial’s own design justification. They give participants per arm for 80% power and participants per arm for 90% power. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

For planning at 100% of the observed effect, the figures are 2,840 participants per arm for 80% power and 3,801 participants per arm for 90% power. For planning at 75% of the observed effect, they are 5,204 participants per arm for 80% power and 6,965 participants per arm for 90% power. For planning at 50% of the observed effect, they are 12,055 participants per arm for 80% power and 16,138 participants per arm for 90% power.

The 80% power column means the illustrative sample size that would give an 80% chance of detecting the specified effect under the listed assumptions, if those assumptions hold. The 90% column describes the corresponding target for a 90% chance. These are planning illustrations, not observed power. Smaller effects require more participants to detect under otherwise unchanged assumptions, which is why the figures increase as the effect fraction decreases.

The registry’s original sample-size assumptions and justification are not reported in the registry record. The planning figures should not be read as the target or achieved enrollment for this trial, and they do not establish that the trial was designed to detect the effect used in the illustration. The paired-eye design and the method used to account for the within-subject relationship are not incorporated in the assumptions described for these figures.

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 = 0.082; treatment proportion p₁ = 0.062; average p̄ = 0.072.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3658 = 0.7170.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3656 = 0.3077.
4. n = (0.7170 + 0.3077)² / (-0.0192)² = 2,839.1, rounded up to 2,840 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 <- 0.0817307692307692                          # control proportion
p1 <- 0.0625                          # 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(2782676)
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 = 2,840 (80% power), 3,801 (90% power)
 75% of observed effect: n per arm = 5,204 (80% power), 6,965 (90% power)
 50% of observed effect: n per arm = 12,055 (80% power), 16,138 (90% power)
power.prop.test: 2839.1 
Simulated power at n = 2,840 per arm: 0.800 (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 lists 12 outcome measures and 10 posted secondary outcomes. Those outcomes cover several kinds of information, including ocular serious adverse events, mean change in intraocular pressure from baseline, a pressure-spike rate at 3 months, and inflammation grades. The primary outcome is the cumulative count of participants with pressure spikes of 30 mmHg or greater during 3 months.

When many outcomes are examined, the chance of finding at least one apparently notable result can increase if each is tested separately. In general, multiplicity methods can adjust interpretation or control an error rate across a family of comparisons. Whether such adjustment is appropriate depends on the prespecified objectives and analysis plan. The registry record does not report a multiplicity strategy, a hierarchy for testing secondary outcomes, or a family of comparisons used for formal inference.

The record indicates no posted analysis records, despite the presence of a displayed primary comparison and outcome results. It does not provide the full statistical analysis plan, including the intended treatment of secondary outcomes, any interim analyses, or the original sample-size justification. These details are not reported in the registry record and should not be inferred from the displayed results.

Missing-data methods are also not described in the registry record. The primary outcome population is identified as paired-eye subjects in the safety population, and the record says this differs from the total participant safety population used in Participant Flow. The reasons for this difference, the number of endpoint observations unavailable, and any imputation or sensitivity analysis are not reported. This limits assessment of whether missingness could affect the interpretation.

The paired-eye design raises a separate analysis question. A method that accounts for the relationship between fellow eyes may be needed for appropriate uncertainty estimation. The record does not report how pairing was handled, whether any subjects contributed only one evaluable eye, or whether sensitivity analyses examined the effect of the analysis population. Without those details, the posted comparison can be described but not fully audited against the study design.

14. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: elevated iop/iop spike (30 mmhg or greater) (8.5%), iop spike <30 mmhg, requiring treatment (1.4%), conjunctival laceration (0.5%), cystoid macular edema (0.5%), mild tass (toxic anterior segment syndrome) (0.5%).

The registry reports serious adverse event counts for the investigational and approved devices separately. For the investigational device, the serious adverse event population at risk is 211 and the number with a serious adverse event is 24. For the approved device, the population at risk is 210 and the number with a serious adverse event is 24. Deaths are recorded as 0 in each group.

The record also gives other adverse event counts: 174 among 211 at risk for the investigational device, and 173 among 210 at risk for the approved device. These are separate from the serious-event counts. The registry lists elevated IOP/IOP spike of 30 mmHg or greater at 8.5% among the top serious-event terms, followed by IOP spike below 30 mmHg requiring treatment at 1.4%. Conjunctival laceration, cystoid macular edema, mild TASS, and wound leak are each listed at 0.5%.

These safety figures are descriptive registry results. They do not establish that an event was caused by a device or show how events were adjudicated. The registry record does not provide additional detail about event-level timing, severity beyond the serious-event designation, or the method used for a statistical safety comparison.

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

The posted results describe a randomized, masked, paired-eye comparison of bacterially-derived Healon5 OVD and animal-derived Healon5 OVD. For the primary endpoint, the record reports 17 participants with postoperative pressure spikes of 30 mmHg or greater in the investigational group and 13 in the control group, with 208 in each endpoint group. The displayed comparison has p = 0.448, and its confidence interval crosses zero. These findings describe the observed counts and the uncertainty around the comparison; they do not establish that the devices are equivalent.

The study’s stated objective was non-inferiority, using a margin of 10%. A non-inferiority conclusion depends on the prespecified effect direction, statistical method, and decision rule, not simply on whether a conventional difference test has a large p-value. The registry record does not report a formal non-inferiority conclusion or enough methodological detail to verify one. The result should therefore not be described as demonstrating non-inferiority on the basis of the counts alone.

The endpoint concerns a threshold event over 3 months in the stated paired-eye safety population. It does not summarize all pressure values, the time course of pressure, or all possible safety outcomes. The registry separately lists other outcomes, including serious adverse events, pressure change from baseline, and inflammation grades. A primary-endpoint result cannot stand in for those other measures.

The record also does not fully describe how paired eyes were accounted for statistically, how missing outcomes were handled, or whether multiplicity was addressed across outcomes. These omissions limit how far the displayed comparison can be interpreted as a complete account of the trial’s analysis. The registered results support a focused description of this endpoint and population, not a broader claim about every outcome or setting.

16. Why This Trial Matters Statistically

This trial illustrates why the wording of a clinical question and the statistical comparison must be read together. The primary objective was non-inferiority, not simply a search for any difference between devices. A non-inferiority question is tied to a prespecified margin, here 10%, and requires evaluating uncertainty in the direction relevant to that margin. A conventional p-value alone does not answer that question.

The paired-eye design is another important statistical feature. Each subject received the investigational device in one eye and the control in the fellow eye. This structure can make within-subject comparisons informative, but the observations from the two eyes may be related. The analysis should reflect the design. The registry record does not report how that pairing was handled, so readers cannot verify the link between the design and the displayed uncertainty estimates.

The endpoint also shows the trade-off inherent in threshold outcomes. Counting participants who crossed the 30 mmHg threshold creates a direct event measure, but it leaves out the magnitude and timing of pressure changes. The counts are useful for describing the registered endpoint, yet they do not tell the full clinical or statistical story of pressure measurements.

Finally, outcome populations and safety populations should not be treated as interchangeable. The registry explicitly distinguishes the paired-eye safety population used for the primary outcome from the total participant safety population used in Participant Flow. Attending to that distinction prevents readers from assuming that every count uses the same denominator or population.

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.

The registry record does not report the full statistical analysis plan, the original sample-size justification, or any interim-analysis plan. It also does not report the formal non-inferiority result, despite stating a non-inferiority objective and a 10% margin. This leaves important parts of the primary inference undocumented in the registry record.

The primary endpoint population is described as paired-eye subjects in the safety population and is said to differ from the total participant safety population used in Participant Flow. The record does not explain the reasons for the difference or provide a detailed accounting of missing primary outcome data. Readers therefore cannot assess from this record alone whether exclusions or unavailable observations may have affected the result.

Although the study used a paired-eye design, the statistical method used to account for within-subject dependence is not reported. The comparison’s confidence interval and p-value should not be assigned a particular paired or unpaired method without documentation. The record also does not explain the risk-difference sign convention in plain language.

The trial’s primary endpoint is a binary threshold event over 3 months. The registry record does not provide the distribution of measured pressure values, event timing, recurrence, or duration. Those details would address questions beyond the registered count endpoint. The record lists multiple secondary outcomes but does not report a multiplicity strategy or a hierarchy of inference.

These are limitations of what the registry record documents. They do not establish that the trial failed to conduct a particular analysis or that the missing details altered the findings. They constrain the conclusions that can be drawn from the posted summary alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Clinical Investigation of the Bacterially-Derived Healon5 Ophthalmic Viscosurgical Device (OVD) — NCT02782676.
• Registry record last updated 2025-02-04; status last verified 2025-01.
• Results first posted 2018-05-24.
• 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

The registry describes a completed, prospective, multicenter, randomized, quadruple-masked, parallel-model, paired-eye clinical investigation of bacterially-derived Healon5 OVD versus animal-derived Healon5 OVD for cataract. Each subject was to receive the investigational device in one eye and control in the fellow eye. The record lists enrollment as 241 and identifies the primary outcome timeframe as 3 months.

The primary outcome counts are 17 among 208 for the investigational device and 13 among 208 for the approved control. The comparison reports p = 0.448, while the posted confidence interval crosses zero. The registry states a non-inferiority margin of 10% but does not report a formal non-inferiority conclusion or complete analysis details.

The record lists 12 outcome measures and 10 posted secondary outcomes. It reports serious adverse event counts of 24 in each group and deaths recorded as 0 in each group. The analysis plan, missing-data methods, multiplicity approach, and handling of paired-eye observations are not reported in the registry record.