Safety and Efficacy of a Drug Delivery System in Glaucoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of a Drug Delivery System in Glaucoma (NCT01016691), a randomized phase 2 study. The primary outcome is Mean Change in Intraocular Pressure at Day 1.

2. Clinical Question

3. Trial Design

The registry record describes NCT01016691 as a randomized, double-masked, parallel-group phase 2 trial. Its stated purpose was to evaluate ocular safety and efficacy of a drug-delivery system in open-angle glaucoma or ocular hypertension. The record lists enrollment of 47 participants and identifies Vistakon Pharmaceuticals as the sponsor. The study status is completed, with a recorded start of 2009-10 and primary completion of 2010-02.

The three reported groups received a high-dose drug device, a low-dose drug device, or a placebo device. The high-dose device contained 65 micrograms of bimatoprost released over 4 days; the low-dose device contained 45 micrograms released over 4 days. The placebo device was worn over 4 days. Each arm description also specifies bimatoprost 0.03% ophthalmic solution for one day in a second period. The record does not explain the rationale for this sequence or provide additional detail about the timing of each measurement relative to the periods.

Random allocation is intended, in general, to reduce systematic differences between groups at the outset. Masking can reduce some influences of knowledge about assigned treatment on care or outcome assessment. The registry record labels the trial double-masked but does not identify which parties were masked or describe how masking was maintained. It also does not report the allocation ratio, the randomization procedure, or the trial's original sample-size justification.

The primary endpoint was mean change in intraocular pressure from baseline to Day 1, in the per-protocol population. The listed secondary outcomes were mean change in intraocular pressure at Day 2, Day 3, Day 4, and Day 5. These results concern a short measurement window; longer-term outcomes are not described in the posted results.

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: per-protocol population

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 Change in Intraocular Pressure at Day 1, measured over Baseline to Day 1.

The primary endpoint is mean change in intraocular pressure from baseline to Day 1, measured in mmHg. It is described as a continuous outcome, reported as a mean with standard deviation, and assessed in the per-protocol population. Change scores express how the measurement at follow-up differs from the participant's baseline measurement. A negative mean change indicates a decrease from baseline for the group; it is not a comparison between the groups by itself.

Intraocular pressure is the clinical measurement selected for this study of glaucoma and ocular hypertension. Comparing change from baseline can account for the starting measurement in describing the outcome, while comparing the groups' changes addresses whether the observed shifts differed across assigned regimens. The posted arm means are -4.16 for the high-dose device regimen, -4.57 for the low-dose device regimen, and -0.6 for the placebo-device regimen. The listed unit is mmHg.

The registry record also lists mean change in intraocular pressure at Day 2, Day 3, Day 4, and Day 5 as secondary outcomes. A primary endpoint gives the study a specified main outcome and time point for interpretation. The record does not report why Day 1 was selected as primary, a threshold for a clinically important change, or details of how the endpoint was measured. The endpoint therefore describes a measured short-term pressure change, not all aspects of ocular safety, longer-term effects, or patient experience.

7. Results Posted in the Registry

• High Dose Drug Device/ Bimatoprost 0.03%: mean -4.16 versus -0.60 on control; difference -3.56 (95% CI -5.70 to -1.42), standardized effect d = -1.23; z-test p = 0.001.
• Low Dose Drug Device / Bimatoprost 0.03%: mean -4.57 versus -0.60 on control; difference -3.97 (95% CI -6.43 to -1.51), standardized effect d = -1.35; z-test p = 0.002.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: intraocular pressure can take a range of measured values, and the registry reports group means and standard deviations. The primary summary is the mean change from baseline to Day 1. A change score is formed by comparing a follow-up measurement with baseline for each participant and then summarizing those changes across the analysis group. A negative group mean indicates that measurements were lower on average at the follow-up point than at baseline. The registry record does not provide the exact measurement procedures or details of how baseline and Day 1 values were combined when observations were unavailable.

What does a mean difference describe?

A mean difference compares the average change in one group with the average change in another group. The posted comparison is against the placebo-device regimen. The high-dose estimate is -3.56 mmHg, based on group means of -4.16 and -0.6. The low-dose estimate is -3.97 mmHg, based on group means of -4.57 and -0.6. These comparison estimates describe the difference in average change, not a change experienced by every participant. Individual responses can vary around a group mean, as the reported standard deviations indicate.

Because lower values of change are more negative, the negative comparison estimates mean that the average change was more negative in each active device group than in the comparator group. The estimates are not direct high-dose versus low-dose comparisons. Nor do they isolate a device effect from every other component of the regimen: all three arm descriptions include bimatoprost 0.03% ophthalmic solution for one day in a second period.

What does a standard deviation add?

A standard deviation describes the spread of participant measurements around a group mean. The reported standard deviations are 3.409 for the high-dose group, 3.645 for the low-dose group, and 2.331 for the placebo-device group. Larger dispersion means that measurements are more varied around the average. This information helps distinguish a group average from a uniform response, but it does not show the full shape of the data or identify outliers. The registry record does not report distribution plots or individual-level observations.

A standard error, in contrast, describes the sampling uncertainty of an estimate such as a mean. Confidence intervals for the comparison estimates incorporate uncertainty in the difference. The record gives comparison intervals and unadjusted p-values, but does not report a detailed statistical model, degrees of freedom, or the confidence level used for those intervals. Those unreported details should not be inferred from the summaries alone.

How should the p-values be read?

The posted unadjusted p-values are 0.001 for the high-dose comparison and 0.002 for the low-dose comparison. In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of a statistical procedure. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or clinical importance of an effect. The record labels these values unadjusted; it does not report a correction for considering multiple outcomes or comparisons. Their interpretation should therefore remain tied to the comparisons as posted rather than treated as a complete account of confirmatory evidence.

The confidence intervals provide a range of values compatible with the estimate under the procedure used. Their width reflects precision: broader intervals allow a wider range of underlying differences, while narrower intervals constrain that range more. Both posted intervals lie below zero, but the record does not state the confidence level or the inferential procedure. Statistical interpretation should retain that limitation rather than attaching an unreported confidence level.

What can be inferred from randomization and masking?

In general, random allocation helps prevent systematic selection of participants into groups and can support a fair comparison, especially when the allocation process is properly implemented. The trial is labeled randomized, but the method used to generate and conceal assignments is not reported in the registry record. Double masking can reduce bias from awareness of assignment, but the masked parties and procedures are not described. These design labels are useful context, not a replacement for details about implementation.

The primary outcome population is identified as per protocol. In general, a per-protocol analysis includes participants meeting specified adherence or eligibility criteria after assignment; exact criteria vary by protocol. The registry record does not state the criteria used or explain how exclusions were handled. Consequently, these results should not be described as an intention-to-treat analysis. The record also does not report a missing-data method, a statistical analysis plan, interim analyses, or the original sample-size rationale. These omissions limit the ability to reproduce or fully audit the inferential approach from the registry record alone.

10. Confidence Intervals and Precision

The high-dose comparison estimate is -3.56 mmHg, with a confidence interval from -5.7 to -1.42. The low-dose estimate is -3.97 mmHg, with a confidence interval from -6.426 to -1.514. In both cases, the interval lies below zero. The interval describes uncertainty around the estimated between-group difference under the analysis procedure used. It does not describe the range of individual participant changes, which is better reflected by the arm standard deviations.

Confidence intervals are useful because they show a range of estimates that remain compatible with the observed data and the method's assumptions. A narrow interval indicates greater precision; a wide interval indicates less precision. The intervals cover multiple possible magnitudes of difference, so the point estimates should not be treated as exact effects. The registry record does not report the confidence level or sufficient methodological detail to identify the interval procedure, so neither should be assumed.

The unadjusted p-values are 0.001 for high dose and 0.002 for low dose. They accompany the estimates but do not convey the size of the difference or its clinical relevance. Interpretation also needs to account for the two active-versus-comparator comparisons and the listed secondary outcomes. Whether a multiplicity procedure was planned or applied is not reported in the registry record. The reported precision is therefore best read as uncertainty for each posted comparison, not as a guarantee about results across every outcome or analysis.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed comparison effects, not the original trial's design assumptions. The calculation assumptions 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. The registry record does not report the trial's own original sample-size justification or assumptions.

For the high-dose comparison, planning for 100% of the observed effect gives 11 participants per arm for 80% power and 14 participants per arm for 90% power. Planning for 75% gives 19 participants per arm for 80% power and 25 participants per arm for 90% power. Planning for 50% gives 42 participants per arm for 80% power and 56 participants per arm for 90% power.

For the low-dose comparison, planning for 100% of the observed effect gives 9 participants per arm for 80% power and 12 participants per arm for 90% power. Planning for 75% gives 16 participants per arm for 80% power and 21 participants per arm for 90% power. Planning for 50% gives 35 participants per arm for 80% power and 47 participants per arm for 90% power.

Power is the chance, under the calculation assumptions and a particular true effect, of detecting an effect at the selected significance level. The 80% column represents a planning target of 80% power; the 90% column represents a higher planning target of 90% power. The smaller effect scenarios require more participants per arm than the larger effect scenarios. These figures are not observed power; they are planning illustrations anchored to the observed estimates, which may not represent the true effect in a future study.

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

Worked calculation for this trial

1. Observed difference Δ = -3.560; pooled standard deviation σ = 2.900.
2. n = 2 × (1.96 + 0.842)² × 2.900² / -3.560² = 10.4, 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 <- -3.56                      # observed difference in means
sigma <- 2.90048850930194                     # 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(1016691)
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), 14 (90% power)
 75% of observed effect: n per arm = 19 (80% power), 25 (90% power)
 50% of observed effect: n per arm = 42 (80% power), 56 (90% power)
power.t.test: 11.5 
Simulated power at n = 11 per arm: 0.782 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint, mean change in intraocular pressure at Day 1, and four secondary pressure-change outcomes at Day 2, Day 3, Day 4, and Day 5. The record also gives comparisons of each active device regimen with the placebo-device regimen for the primary outcome. Considering multiple outcomes or comparisons raises a general multiplicity issue: when many statistical tests are examined, the chance of at least one apparently unusual result can increase. A prespecified strategy may address that issue, but such a strategy is not reported in the registry record.

The listed p-values are unadjusted. No multiplicity adjustment, hierarchy for testing outcomes, or distinction between confirmatory and exploratory analyses is reported. The p-values should therefore be understood as unadjusted results for the individual comparisons, rather than as evidence that the overall family of outcomes was controlled for repeated testing. The registry record does not provide numeric results for the secondary outcomes in the registry record, so their relationship to the primary endpoint cannot be assessed from the posted primary summaries.

The primary population is described as per protocol. The criteria used to define that population, the number excluded from it, and the reasons for any exclusions are not reported in the registry record. Missing-data methods, handling of withdrawals, and whether any sensitivity analyses were conducted are also not reported. These details matter because exclusions and unavailable measurements can affect which participants contribute to an estimate.

The record identifies the study as randomized and double-masked but does not report the randomization procedure, masked parties, allocation concealment, or a statistical analysis plan. Interim analyses and stopping rules are not reported. The registry record also does not report the original sample-size justification. The posted comparisons and planning illustrations can be described on their own terms, but they do not fill these gaps in the trial's planned analysis or its handling of missing data.

14. Safety Results

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

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The serious adverse event summaries report zero affected participants in each group: the high-dose device group lists 0 of 17 at risk, the low-dose device group lists 0 of 12 at risk, and the placebo-device group lists 0 of 18 at risk. These are counts for the registry's serious adverse event summary. The record lists no serious adverse event terms. The death counts are not reported in the registry record, so they should not be interpreted as zero.

Separately, the other adverse event summaries list 12 of 17 at risk for the high-dose group, 7 of 12 for the low-dose group, and 8 of 18 for the placebo-device group. These are not serious adverse event counts and should not be conflated with the serious-event figures. The summary does not provide event descriptions in the registry record used here, severity details for these other events, timing, or event-level counts. The adverse event denominators also differ from the per-protocol group sizes reported for the primary endpoint; the registry record does not explain the relationship between those populations. These summaries describe reported counts and do not, on their own, establish comparative safety.

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

The posted primary endpoint results show mean intraocular pressure changes from baseline to Day 1 of -4.16 mmHg for the high-dose device regimen, -4.57 mmHg for the low-dose device regimen, and -0.6 mmHg for the placebo-device regimen. The corresponding active-versus-comparator estimates are -3.56 mmHg and -3.97 mmHg, with confidence intervals from -5.7 to -1.42 and from -6.426 to -1.514. These values describe the short-term comparisons in the per-protocol population.

These results do not establish that the high-dose regimen differs from the low-dose regimen, because a direct comparison between those active groups is not reported. Nor do they isolate the device component from the full regimen: the descriptions for all three groups include bimatoprost 0.03% ophthalmic solution for one day in a second period. The reported endpoint is pressure change, not a complete measure of ocular health, long-term outcomes, or participant experience.

The results also do not establish how outcomes would differ in other populations, under different treatment sequences, or over a longer follow-up period. The registry record does not report the details needed to assess missing observations, population exclusions, or multiplicity adjustment. The statistical intervals indicate uncertainty around each estimate, while the standard deviations indicate variation among measurements. Neither should be mistaken for proof that every participant had the group-average change.

Statistical evidence and clinical importance are not interchangeable. The record does not report a threshold for a clinically important difference, so the magnitude's clinical meaning cannot be determined from these summaries alone. No medical advice follows from the posted results. They are best understood as estimates from a completed, randomized, double-masked phase 2 study with a short-term primary endpoint and the limitations described in the registry record.

16. Why This Trial Matters Statistically

This trial illustrates why the analysis population and the measured time point matter when reading clinical results. The primary outcome is explicitly a per-protocol mean change from baseline to Day 1. That is a defined short-term summary, not necessarily a description of all randomized participants or of later outcomes. The registry record does not report how the per-protocol population was formed, which makes the population definition an important limitation rather than a minor technical detail.

It also demonstrates the difference between a within-group change and a between-group contrast. The arm means describe change within each regimen, while the comparison estimates place each active device regimen against the placebo-device regimen. The estimates and intervals make the contrast more informative than reading group means in isolation. At the same time, a comparison against the shared comparator is not a direct comparison of the two active doses.

Precision and multiplicity are relevant as well. The confidence intervals show a range around each estimated difference, and the unadjusted p-values address the individual comparisons as posted. The record lists additional secondary time points but does not report whether a multiple-testing strategy was used. Thus, the primary estimates have to be considered alongside the analysis details that are absent, not read as a complete statistical account.

Finally, the planning illustrations make visible how sample-size requirements depend on the assumed effect and desired power. They use the observed effect as a planning anchor and show larger planning requirements for smaller effects. They are not the trial's original design rationale, which is not reported. Together, these features offer a practical example of how effect estimates, uncertainty, analysis populations, and planning assumptions answer different statistical questions.

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 randomization procedure, allocation concealment, or the parties masked in this double-masked study. It provides no detailed schedule linking the primary Day 1 endpoint to the device and solution periods. Although each arm description specifies a device period followed by one day of bimatoprost 0.03% ophthalmic solution, the record does not explain the purpose of that sequence or how it relates to the endpoint timing.

The primary analysis population is per protocol, but the record does not define its eligibility or adherence criteria, explain exclusions, or provide an all-randomized-participant analysis. Missing-data methods and sensitivity analyses are not reported. The arm sample sizes for the primary endpoint and the at-risk counts in the safety summaries differ, and the record does not explain the population or accounting differences. They should not be assumed to represent the same analysis sets.

The registry record does not provide numeric results for the listed secondary outcomes in the registry record used for this analysis, nor does it report a multiplicity strategy. It also does not report a confidence level or detailed inferential procedure for the comparison intervals. The original sample-size rationale, interim analyses, and formal statistical analysis plan are not reported. These omissions constrain assessment of whether the posted comparisons followed a prespecified approach.

Finally, the primary outcome is measured over a short period, and the registry entries do not include longer-term results or a clinically important difference threshold. The serious adverse event summary reports zero affected participants in the listed groups, but death counts are not reported in the registry record. The other adverse event counts are available without event-level details in the registry record. Consequently, the posted data support a limited account of short-term pressure changes and reported event counts, not a broad conclusion about durability or comparative safety.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy of a Drug Delivery System in Glaucoma — NCT01016691.
• Registry record last updated 2015-03-06; status last verified 2015-02.
• Results first posted 2012-01-27.
• 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

NCT01016691 is a completed randomized, double-masked, parallel-group phase 2 trial sponsored by Vistakon Pharmaceuticals. It enrolled 47 participants with open-angle glaucoma or ocular hypertension. The record gives a start of 2009-10 and primary completion of 2010-02.

The reported regimens were high-dose drug device, low-dose drug device, and placebo device; each arm description also includes bimatoprost 0.03% ophthalmic solution for one day in a second period. The primary endpoint was mean change in intraocular pressure from baseline to Day 1, in the per-protocol population. The posted comparisons versus the placebo-device regimen were -3.56 mmHg for high dose and -3.97 mmHg for low dose, with unadjusted p-values of 0.001 and 0.002.

The registry record lists secondary pressure-change outcomes at Day 2, Day 3, Day 4, and Day 5. Serious adverse event summaries list zero affected participants in each group; deaths are not reported in the registry record. Details of the analysis plan, missing-data handling, multiplicity strategy, and original sample-size justification are not reported in the registry record.