Corneal Staining and Physiological Compromise After Eight Hours of Soft Contact Lens Wear: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Corneal Staining and Physiological Compromise After Eight Hours of Soft Contact Lens Wear (NCT01015768), a randomized na study. The primary outcome is The Primary Outcome Measure Will be Corneal Epithelial Dye Diffusion Rate in Nanometers Per Second, for the Test and Control Eyes..

2. Clinical Question

The clinical question concerns short-term corneal measurements after lens wear under the two recorded eye conditions. The primary measure is a dye diffusion rate, intended to reflect movement of fluorescein from tears into corneal tissue. The secondary measure is a corneal staining grade, with the registry describing comparisons between test and control eyes and between baseline and final staining for each eye.

The study is recorded as randomized and triple-masked, but those labels do not specify how the randomization was carried out, who was masked, or how the eye conditions were assigned. Those details are not reported in the registry record. The clinical question is therefore best read as a comparison of the recorded test-eye and control-eye conditions, rather than as evidence isolating a single component of lens care.

3. Trial Design

The registry identifies this as a randomized, triple-masked study with a single-group model. It records enrollment of 30 and a completed status. The study dates are recorded as starting in 2009-10, with primary completion in 2010-01. The phase is listed as NA. The sponsor is Southern California College of Optometry at Marshall B. Ketchum University.

The comparison is described in terms of a test eye and a control eye. The test eye used ReNu Multiplus as a multipurpose soaking solution. The control condition used a new PureVision lens soaked for 2 hours in non-preserved saline. Both primary and secondary outcomes were assessed after eight hours of wear. While the study is labelled randomized, the randomization procedure and the way the eye conditions were allocated are not reported in the registry record.

The primary outcome summary is identified as per protocol and includes 26 observations in each eye group. The secondary outcome summaries include 30 observations in each group. The record does not explain this difference in analysis counts or report participant flow, exclusions, or reasons for missing measurements. It also does not describe whether the statistical comparison accounted for the possibility that measurements from two eyes of the same participant may be related.

The registry describes a comparison of eye conditions, but the lens and soaking conditions differ in more than the solution name: the control description specifies a new lens and a saline soak. The posted results therefore characterize the recorded conditions as a whole. The registry does not establish that any observed contrast can be attributed to the solution alone.

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: Eyes were randomized to one of two conditions.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was per protocol.

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 The Primary Outcome Measure Will be Corneal Epithelial Dye Diffusion Rate in Nanometers Per Second, for the Test and Control Eyes., measured over After eight hours of wear.

The primary endpoint is the mean corneal epithelial fluorescein dye diffusion rate, expressed in nanometers per second, after eight hours of wear. The registry describes fluorescein as moving from tears, where its concentration is high, into the cornea, where its concentration is low. The rate is intended to reflect how the corneal epithelium limits, or does not limit, that movement.

This measure is used as an indicator of corneal epithelial barrier behavior. In general, a measured diffusion rate can provide information about a biological process that is not captured by a visual grade alone. It remains a measurement of dye movement, however, rather than a direct diagnosis or a complete measure of corneal health. The registry does not state a threshold for interpreting a particular rate as normal, abnormal, or clinically important.

The endpoint is summarized as a mean with standard deviation. The registry reports a mean of 0.057 and standard deviation of 0.039 for the PHMB-containing disinfectant condition, and a mean of 0.058 and standard deviation of 0.038 for non-preserved saline. The posted comparison is a mean difference of 0.002, with an interval from -0.019 to 0.022 and an unadjusted p-value of 0.881. The confidence level for the interval is not reported in the registry record.

The endpoint description makes the biological rationale clear, but does not provide a clinical threshold or specify how small a difference would matter. Consequently, the numerical contrast describes the measured diffusion rates; it does not by itself establish a clinically meaningful change.

7. Results Posted in the Registry

• Non-preserved Saline: mean 0.06 versus 0.06 on control; difference 0.00 (95% CI -0.02 to 0.02), standardized effect d = 0.04; z-test p = 0.881.

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.

The Secondary Outcome Measure Will be the Corneal Staining Grade, Compared Between the Test and Control Eye, as Well as Between the Baseline and Final Staining for Each Eye.

• 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:
  • Non-preserved Saline: mean 4.52 versus 4.95 on control; difference -0.43 (95% CI -1.60 to 0.74), standardized effect d = -0.19; z-test p = 0.469.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-preserved Saline and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is corneal staining grade after eight hours of wear. Its group summaries and comparison describe a point estimate in the direction of lower average staining for the non-preserved saline condition, but the interval includes zero and the unadjusted p-value does not establish a clear difference. The secondary result does not overturn or resolve the primary outcome finding: both are comparisons with uncertainty that includes no difference.

The two measures address related but distinct aspects of the corneal response. The primary endpoint concerns fluorescein dye diffusion through the epithelial barrier, while the secondary outcome concerns a staining grade. A similar lack of a clearly established contrast across these measures is a broad descriptive pattern, not proof that the underlying processes are identical or that one measure validates the other.

The registry describes baseline and final staining comparisons for each eye, but the posted secondary results present the endpoint summaries and the comparison after eight hours. Detailed baseline values and the analysis of change from baseline are not reported in the registry record. It is therefore not possible to assess from the posted summary whether changes over time differed between conditions.

The secondary outcome should carry less inferential weight than a fully specified primary analysis. The registry reports an unadjusted p-value and does not describe a prespecified testing hierarchy or correction for multiple outcomes. It lists three outcome measures but posts one secondary outcome. How the other outcome measures were handled is not reported. When several measures are considered, an isolated result can be more vulnerable to chance findings, so the secondary evidence is best treated as supportive and exploratory rather than definitive.

These comparisons also inherit the design and reporting limitations that affect the primary result. The analysis method, handling of any within-participant eye correlation, and missing-data procedures are not reported. The secondary summaries add useful description of staining, but they do not answer those methodological questions.

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

• The Secondary Outcome Measure Will be the Corneal Staining Grade, Compared Between the Test and Control Eye, as Well as Between the Baseline and Final Staining for Each Eye.

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports continuous outcomes as means and standard deviations. A mean describes the central value of the observations, while a standard deviation describes how dispersed observations are around that mean. These summaries help describe the outcome distribution, but they do not show the individual measurements or establish that the distribution has any particular shape.

Comparing two means

The primary comparison is presented as a mean difference between the non-preserved saline and PHMB-containing disinfectant conditions. The posted estimate is 0.002. The comparison therefore summarizes the separation between the reported group means on the outcome scale. The direction of a difference depends on which condition is subtracted from which; the registry’s displayed estimate and group means indicate the contrast as saline relative to the PHMB-containing disinfectant condition.

In general, a mean difference expresses a contrast in the original measurement units, which are nanometers per second. It can be easier to interpret in context than a standardized measure because it retains the endpoint’s scale. But a numerical contrast alone does not indicate clinical importance. The registry does not report a threshold for a meaningful difference in diffusion rate.

Uncertainty and p-values

A confidence interval expresses uncertainty around an estimated contrast. In general, an interval is produced by a method with a specified long-run coverage property under its assumptions; it is not a range guaranteed to contain the true value, nor is it a probability statement about the true value after observing the data. The confidence level and the method used for the posted intervals are not reported in the registry record. The primary interval extends from -0.019 to 0.022.

The unadjusted p-value for the primary comparison is 0.881. In general, a p-value describes how unusual data at least as incompatible with a specified null model would be, assuming that model and the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The null model and test details are not specified in the registry record, so the p-value is best treated as a posted unadjusted result rather than a fully documented analysis.

What the analysis counts mean

The primary outcome is described as per protocol, and its summaries use 26 observations per eye condition. The secondary outcome summaries use 30 per condition. Per-protocol analysis generally refers to analyzing participants who meet protocol-related criteria, but the registry does not give the criteria or explain the difference in counts. It does not report an intention-to-treat analysis, reasons for exclusions, or methods for handling missing outcome data.

The study describes test and control eyes. In general, measurements from two eyes of the same participant may be correlated. A statistical method that recognizes this relationship can differ from one that treats all observations as independent. Whether the posted analysis accounted for any within-participant relationship is not reported in the registry record. The comparison method, variance assumptions, and any adjustment for covariates are also not reported.

Why over-dispersion can matter

In general, over-dispersion occurs when observed variability is greater than a model assumes. If a method understates variability, its standard errors may be too small and its intervals too narrow; if it handles variability appropriately, uncertainty estimates can better reflect the data. The posted outcomes are continuous and are summarized using standard deviations, but the registry does not describe a model or report an assessment of over-dispersion. This concept is therefore relevant as a general statistical consideration, not as a documented problem in this study.

Secondary analyses and multiplicity

The registry lists three outcome measures and posts one secondary outcome. It reports unadjusted comparisons and no reported analyses. When several outcomes or contrasts are examined, the chance of at least one apparently notable result can increase. In general, multiplicity procedures can address that issue, but they require a stated analysis plan. No correction for multiple testing or prespecified hierarchy is reported. The secondary result should therefore be treated as less confirmatory than a result from a clearly specified primary analysis with a documented multiplicity strategy.

In general, the most useful assessment combines the effect estimate, its uncertainty, the analysis population, and the assumptions of the method. Here, the registry gives group summaries, an interval, and an unadjusted p-value, but omits important details about the statistical procedure. These omissions limit how far the inferential results can be assessed.

11. Confidence Intervals and Precision

The posted primary mean difference is 0.002, and its interval extends from -0.019 to 0.022. The interval includes zero and reaches in both directions from the point estimate. This indicates that the point estimate should not be read as a precise determination of the direction or size of the contrast. The confidence level and the procedure used to construct this interval are not reported in the registry record.

In general, a confidence interval presents a range of estimates that are compatible with the observed data under the method’s assumptions. A narrower interval indicates greater precision than a wider interval on the same scale. An interval that includes zero does not prove there is no difference; it indicates that zero is among the values not excluded by that interval. The interval also does not establish that all values it covers are clinically unimportant.

The posted primary means and standard deviations describe the observed groups, but precision depends on more than the group means alone. It is affected by the amount of information and variability, as well as by the comparison method. The primary summaries include 26 observations in each condition. The registry does not explain the per-protocol analysis count or report the test used to construct the interval.

The secondary staining interval extends from -1.595 to 0.735 around a mean difference of -0.43. It includes zero as well. Its confidence level and calculation method are also not reported. The intervals therefore support cautious interpretation of both contrasts: neither posted estimate defines a clear directional difference, and neither demonstrates equivalence. A clinical threshold for meaningful change is not reported for either outcome.

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

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to detect the selected effect under those assumptions with 80% power. The 90% power column gives the corresponding number for 90% power. In general, power is the chance that a planned analysis will detect an effect of the specified size if that effect is present and the assumptions hold; it is not a measure of the probability that the result is true.

The scenarios include planning for 100%, 75%, and 50% of the observed effect. The displayed participant requirements increase as the target effect becomes smaller. This is expected in general: a smaller effect is harder to distinguish from variability, so more participants are needed to maintain the same planned power under otherwise unchanged assumptions.

These figures are planning illustrations, not observed power and not evidence that the study was originally designed with these assumptions. They do not account for design features or analysis choices that are not specified in the registry, including whether eye measurements were treated as related. They should be read as conditional calculations, not as a retrospective judgment about whether the completed study was adequately sized.

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 = 0.002; pooled standard deviation σ = 0.039.
2. n = 2 × (1.96 + 0.842)² × 0.039² / 0.002² = 9,090.6, rounded up to 9,091 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 <- 0.0016                      # observed difference in means
sigma <- 0.0385032466163569                     # 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(1015768)
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 = 9,091 (80% power), 12,170 (90% power)
 75% of observed effect: n per arm = 16,162 (80% power), 21,636 (90% power)
 50% of observed effect: n per arm = 36,363 (80% power), 48,679 (90% power)
power.t.test: 9091.6 
Simulated power at n = 9,091 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists three outcome measures, while one secondary outcome is posted. It does not report results for the other outcome measures in the registry record. The primary and secondary comparisons include unadjusted p-values, and no multiplicity adjustment, testing hierarchy, or prespecified strategy for interpreting multiple outcomes is reported. Without a stated plan, the extent to which the reported comparisons were selected from a broader set of analyses cannot be assessed.

Multiplicity matters because examining multiple outcomes or contrasts can increase the chance of observing an apparently unusual result even when there is no underlying effect. In general, a prespecified hierarchy or adjustment can help control that issue. The registry does not state whether such a plan existed, so the secondary result should not be read as confirmatory evidence on its own. The primary result also cannot be evaluated against a complete analysis plan from the record.

The primary outcome population is described as per protocol. The record does not give the criteria for inclusion in that population or explain why the primary group summaries include 26 observations per condition while the secondary summaries include 30. It does not report the number screened, the number who completed each measurement, reasons for missing data, or whether any participants were excluded after randomization.

Missing-data handling is not reported in the registry record. There is no description of imputation, sensitivity analyses, or assumptions about missing outcomes. The record also does not report an intention-to-treat analysis. These omissions mean the influence of exclusions or missing measurements on the reported estimates cannot be judged from the registry summaries.

Finally, the registry does not provide a detailed statistical analysis plan, the precise comparison test, or whether the eye-level structure was incorporated into the analysis. It reports no analyses in its analysis listing, although outcome means and comparisons are posted. This leaves the calculation and inferential framework incompletely documented.

15. 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.

For both the Test Eye and Control groups, the registry reports 30 participants at risk for serious adverse events and 0 affected. It also reports 30 participants at risk for other adverse events and 0 affected in each group. No serious adverse event terms are listed. These figures describe the adverse-event counts recorded in the registry for the groups.

The death counts are not reported in the registry record. The absence of listed serious-event terms and the reported zero affected counts do not establish that no events of any kind occurred outside the definitions or reporting period represented by these entries. The record does not provide additional detail on event definitions, monitoring, severity categories beyond the listed serious and other groupings, or the time period used for adverse-event collection.

These observations come from a study with enrollment of 30 and should be read as descriptive safety reporting, not as a precise estimate of uncommon risks. The registry does not provide a broader safety analysis or enough detail to compare risks beyond the recorded counts.

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

The posted data show that the mean dye diffusion rates were close in the two recorded conditions, with a mean difference of 0.002. The interval from -0.019 to 0.022 includes zero, and the unadjusted p-value is 0.881. The results therefore do not establish a clear difference in the primary endpoint. They also do not prove that the conditions are equivalent or that any possible difference is clinically unimportant.

The staining comparison similarly does not establish a clear difference: its interval includes zero and its unadjusted p-value is 0.469. This is a statement about the posted summary estimates and their uncertainty, not a conclusion about whether either lens-care condition is beneficial or harmful. No threshold for a clinically important change is reported.

The interpretation is limited to the measured outcomes after eight hours of wear under the recorded conditions. The registry does not report participant characteristics that would show how representative the enrolled group was, and it does not provide results for other lens types, solutions, wear schedules, or settings. The control and test descriptions also differ in lens and soaking details, so the comparison cannot isolate the effect of the solution alone.

The record does not give the statistical analysis plan, the method used for the comparisons, the handling of missing data, or whether the analysis accounted for related measurements from test and control eyes. Those omissions limit confidence in assessing the inferential procedure. The posted figures are informative descriptions of this study’s results, but they do not support broader causal or clinical conclusions beyond the recorded comparison.

In general, a result that does not establish a difference should not be translated into proof of no effect. Nor should an estimate be treated as important solely because it points in one direction. The estimate, interval, study design, analysis details, and clinical context all matter; the latter thresholds and several methodological details are not reported in the registry record.

17. Why This Trial Matters Statistically

This study illustrates how statistical interpretation depends on looking beyond a point estimate. The primary mean difference is 0.002, but the interval extends from -0.019 to 0.022. The interval includes zero and permits uncertainty about both the direction and size of the contrast. The unadjusted p-value of 0.881 is consistent with the absence of a clearly established difference, but does not establish equivalence.

The endpoints also show why different measurements should not be collapsed into a single conclusion. Dye diffusion and staining grades capture distinct features of the corneal response. The secondary result does not provide clear evidence of a contrast either, but it is not a substitute for the primary endpoint. Together, the reported measures describe the study’s findings without resolving the clinical importance of small or uncertain differences.

The registry’s reporting makes analysis populations important to notice. The primary outcome is per protocol with 26 observations per condition, whereas secondary summaries use 30 per condition. The record does not explain the difference. That discrepancy in counts does not by itself reveal why measurements are absent, but it signals that population and missing-data details matter when interpreting results.

The study is also a reminder that randomized and masked labels do not fully describe analytic methods. The record does not specify randomization procedures, the exact comparison test, or whether the analysis addressed possible dependence between eyes. These details can affect how uncertainty should be understood. A complete statistical account needs enough information to connect design, analysis population, and estimates.

Finally, planning figures based on an observed effect are not a substitute for the original design justification. The record does not report its original sample-size assumptions. Separating retrospective planning illustrations from prospective design information helps avoid treating calculated requirements as proof of observed power or as evidence about the study’s original intent.

18. Limitations

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

The registry does not report participant characteristics, so the applicability of the results to particular groups cannot be evaluated. It also does not provide detailed information about lens-wear history, eligibility criteria, adherence, or the conditions under which the eight-hour wear period took place. These details may be relevant to interpreting a short-term ocular measurement, but they are not available in the registry record.

The recorded conditions differ in both lens-care solution and lens description: the test eye used ReNu Multiplus, while the control description specifies a new PureVision lens soaked in non-preserved saline for 2 hours. The comparison therefore cannot be interpreted as isolating the effect of solution alone. The registry does not provide further protocol detail to clarify which aspects were intended to differ.

The primary analysis is per protocol, but the record does not explain the reduction from 30 enrolled to 26 observations per condition or identify the reasons for exclusions. Missing-data methods and an intention-to-treat analysis are not reported. The analysis method is also not described, including whether any relationship between measurements from test and control eyes was taken into account.

The registry lists three outcome measures but posts one secondary result. It does not report a multiplicity strategy, a detailed statistical analysis plan, or clinical thresholds for meaningful differences in diffusion or staining. Confidence levels and interval-construction methods are not reported. These limitations constrain the interpretation of both statistical precision and clinical relevance.

Finally, the results concern measurements after eight hours of wear, and the registry does not report longer-term outcomes. The study’s sample and short-term endpoint summaries do not establish what would occur under other lenses, care regimens, wear durations, or clinical circumstances.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Corneal Staining and Physiological Compromise After Eight Hours of Soft Contact Lens Wear — NCT01015768.
• Registry record last updated 2020-09-18; status last verified 2020-08.
• Results first posted 2020-09-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry records a completed, randomized, triple-masked study with a single-group model and enrollment of 30. The comparison involved a test eye using ReNu Multiplus and a control eye using a new PureVision lens soaked in non-preserved saline for 2 hours. Outcomes were assessed after eight hours of wear.

The primary outcome was mean corneal epithelial fluorescein dye diffusion rate. Its posted comparison was a mean difference of 0.002, with an interval from -0.019 to 0.022 and an unadjusted p-value of 0.881. The secondary outcome was corneal staining grade; its posted comparison had an interval including zero and an unadjusted p-value of 0.469.

The primary summaries are per protocol and include 26 observations per condition; the secondary summaries include 30 per condition. The registry does not explain the difference or report detailed analysis methods, missing-data procedures, multiplicity handling, or the original sample-size justification. The posted data describe the measured outcomes but do not establish equivalence or clinical importance.