Evaluating the Impact of JJVC Senofilcon A - Based Contact Lens With New UV-blocker on Day and Night Driving Performance: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluating the Impact of JJVC Senofilcon A - Based Contact Lens With New UV-blocker on Day and Night Driving Performance (NCT03330275), a randomized phase 2 study. The primary outcome is Overall Nighttime Driving Score.

2. Clinical Question

The study examined driving and visual performance during daytime and nighttime conditions, but the primary endpoint was specifically the overall nighttime driving score. Its composite combined six measures of driving performance, including sign recognition, hazard avoidance, pedestrian recognition, lane keeping, and lap time. Each measure contributed equally after transformation to a Z-score, with the direction set so that a positive score represented performance better than the mean.

The design was intended to compare conditions within a randomized crossover study rather than to compare independent groups of drivers. Each subject was assigned an order for the three lens conditions, and the registry also describes randomized driving-time sequence, route, and locations of hazards and pedestrians. These features address the question of performance under different lens conditions in a controlled driving setting; they do not establish how the results would generalize beyond the study setting.

The record names several secondary measures of visual acuity, contrast, sign recognition, hazard avoidance, and pedestrian recognition. Their results can add context to the primary score, but do not replace the primary question or establish effects on outcomes beyond those assessed.

3. Trial Design

This was a Phase 2, randomized, single-masked, crossover study sponsored by Johnson & Johnson Vision Care, Inc. The registry describes a bilateral, non-dispensing study with four visits and a three-period, three-treatment crossover. Enrollment was 24. The study status is completed; the registry records a start date of 2017-09-27 and primary completion date of 2017-12-11.

In a crossover design, subjects receive more than one study condition in an assigned sequence. This allows measurements under different conditions to be made in the same subject, so subject-level characteristics that remain stable can be shared across comparisons. The record lists six possible orders for the three lens conditions. It also describes randomization of the day/night driving sequence and route, with hazard and pedestrian locations randomized for each route.

Testing took place on a closed-road driving circuit, during both daytime and nighttime conditions, under challenging driving conditions. The primary outcome was nighttime driving performance. The reported timeframe for the primary and listed secondary measures was 15 Minutes Post Lens Fitting. The primary analysis population was described as all subjects who completed the study without a major protocol violation.

The registry does not report the eligibility criteria, the full visit schedule, details of lens fitting or washout between conditions, or the specific masking arrangements beyond subject masking. It also does not report the planned sample-size justification or the original statistical analysis plan. Period effects, sequence effects, and any assessment of carryover are not described in the registry record. Those omissions limit how fully the conduct and analysis of this crossover design can be evaluated from the record 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: A 2X2 William's crossover design was utilized for visit 1. A 3X3 William's Crossover design was utilized for visits 2, 3 and 4.

Only the first 6 of 10 groups are shown.

Visit 1 - Period 1

Visit 1 - Period 2

Visits 2, 3 and 4 - Period 1

Visits 2, 3 and 4 - Period 2

Analysis population for the primary outcome, as defined in the registry: All subjects that completed the study without a major protocol violation.

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 Overall Nighttime Driving Score, measured over 15 Minutes Post Lens Fitting.

The primary endpoint was the Overall Nighttime Driving Score, measured as a Z-score 15 Minutes Post Lens Fitting. It was a composite rather than a single driving task. The score averaged the Z-scores for six measures: average sign recognition distance, percentage of correctly identified signs, hazard avoidance or detection, pedestrian recognition distance, lane keeping, and the inverse of driving lap time. The registry states that each measure received equal weight.

Combining measures can represent several aspects of performance in one outcome, rather than treating one task as a complete summary of driving. The transformations also put measures with different original units onto a common standardized scale. The Z-scores were oriented so that positive values indicated performance better than the mean. A score below zero therefore indicates a value below the mean on this composite scale; it does not, by itself, describe the practical importance of the difference.

A composite can be useful when the clinical question concerns overall performance across related tasks. At the same time, its interpretation depends on the choice and weighting of component measures. Equal weighting means that the six components contributed equally to the score, not that they are interchangeable or equally important in every driving context. The registry does not report a threshold for a meaningful difference on the composite, so the clinical importance of a particular score difference cannot be determined from the endpoint definition alone.

7. Results Posted in the Registry

• Test: mean -0.31 versus -0.38 on control; difference 0.07 (95% CI -0.19 to 0.32), standardized effect d = 0.15; z-test p = 0.609.
• Control 2: mean -0.43 versus -0.38 on control; difference -0.05 (95% CI -0.31 to 0.20), standardized effect d = -0.12; z-test p = 0.676.

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.

Binocular Visual Acuity

• 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:
  • Test: mean 0.25 versus 0.27 on control; difference -0.02 (95% CI -0.06 to 0.02), standardized effect d = -0.31; z-test p = 0.286.
  • Control 2: mean 0.30 versus 0.27 on control; difference 0.02 (95% CI -0.02 to 0.07), standardized effect d = 0.35; z-test p = 0.230.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Control 2 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Road Signs Correctly Identified During Night Driving

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Test: 70.8% (17/24) versus 75.0% (18/24) on control; risk difference -4.2 percentage points (95% CI -29.3 to 20.9), risk ratio 0.94 (0.67–1.33); unadjusted two-proportion z-test p = 0.745.
  • Control 2: 75.0% (18/24) versus 75.0% (18/24) on control; risk difference 0.0 percentage points (95% CI -24.5 to 24.5), risk ratio 1.00 (0.72–1.39); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Control 2 and the control. The interval gives the range of effects that remain compatible with the data.

Average Distance to Correctly Identify Road Signs During Night Driving

• 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:
  • Test: mean 110.30 versus 101.50 on control; difference 8.80 (95% CI -5.07 to 22.67), standardized effect d = 0.36; z-test p = 0.214.
  • Control 2: mean 95.00 versus 101.50 on control; difference -6.50 (95% CI -20.20 to 7.20), standardized effect d = -0.27; z-test p = 0.352.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Control 2 and the control. The interval gives the range of effects that remain compatible with the data.

The registry names secondary outcomes spanning visual acuity, contrast threshold, road-sign recognition, hazard avoidance, and pedestrian recognition. Numerical results are available for binocular visual acuity, the percentage of road signs correctly identified, and average sign-recognition distance. The record does not provide numerical result details for the other named secondary outcomes. The available outcomes use different scales and summarize distinct tasks, so their estimates should not be collapsed into a single overall effect.

Across the outcomes with numerical detail, the unadjusted estimates do not point uniformly in one direction relative to Control 1: the posted Test comparison is lower for visual acuity on the logMAR scale and for the percentage of signs correctly identified, while the average sign-recognition distance estimate is higher. The intervals for these unadjusted comparisons include zero. This mix does not establish a consistent pattern of improved or worsened performance across visual and driving measures. Nor does it overturn the uncertainty in the primary nighttime composite.

The registry also reports sponsor analyses for visual acuity, correct sign identification, and sign-recognition distance. Those analyses use model-based methods and include labels of NON INFERIORITY or EQUIVALENCE. The margins and full decision rules are not reported, so those labels alone do not permit an independent assessment of whether the relevant criteria were met.

Secondary endpoints often provide supportive context, but multiple outcomes create multiple opportunities for a finding to appear noteworthy by chance. The registry does not report whether multiplicity was controlled, whether secondary outcomes were prespecified in a hierarchy, or whether the reported analyses were confirmatory. For that reason, unadjusted secondary comparisons carry less weight than a clearly specified primary analysis, especially when several measures and comparisons are considered together. The results are best read as exploratory context rather than as separate proof of an effect.

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

• Binocular Visual Acuity
• Binocular Contrast Threshold Without Glare
• Percentage of Road Signs Correctly Identified During Night Driving
• Average Distance to Correctly Identify Road Signs During Night Driving
• Percentage of Hazards Avoided During Night Driving
• Average Pedestrian Recognition Distance

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean score on a standardized composite scale. A mean describes the central value of observations, while the standard deviation describes how dispersed individual values are around that mean. The posted arm summaries give the mean and standard deviation for each lens condition. The group means alone do not show how much individual subjects varied, and the standard deviations do not describe the uncertainty in a treatment contrast by themselves.

What does a mean difference represent?

A mean difference is the estimated contrast between the mean in one condition and the mean in its comparator. The direction depends on the order of subtraction. For the posted unadjusted Test-versus-Control 1 calculation, the reported difference is 0.067; a positive value means the Test mean was higher on the oriented Z-score scale in that calculation. The comparison with Control 2 is -0.055, indicating the opposite direction. These contrasts are not adjusted for the crossover structure. The sponsor’s Linear Mixed Model is the registry-reported model-based analysis for Test versus Control 1.

In general, a mixed model can account for correlations among repeated measurements from the same subject and can include design-related terms. However, the registry does not report the model specification, covariance structure, included terms, or estimation details. It is therefore not possible to determine precisely how the sponsor model handled each feature of the crossover design. A simple calculation from arm-level means and standard deviations treats the posted summaries as the basis for an unadjusted contrast; it does not recover all information from the repeated-measures data.

Why are confidence intervals useful?

In general, a confidence interval expresses uncertainty around an estimated effect under the assumptions of its analysis. It shows a range of values compatible with the data and method, rather than proving that the true effect lies within a fixed set of values. An interval that includes zero is compatible with no difference, as well as with effects in either direction within the interval. It is not, on its own, proof of equivalence. To establish equivalence or noninferiority, an analysis ordinarily depends on a prespecified margin and a method for comparing the interval with that margin; the registry does not report the margin for the primary noninferiority analysis.

The sponsor’s reported primary interval is labeled 95%, with bounds of -0.045 and 0.183. The unadjusted recalculation has a broader interval, from -0.19 to 0.324. These intervals arise from different analyses, so their widths should not be taken as a direct measure of a disagreement about the underlying trial. The simple calculation does not model within-subject correlation as the sponsor’s crossover analysis may do; the specific model details are not reported. For the same reason, the unadjusted p-value of 0.609 is not the p-value for the sponsor model. No sponsor p-value is reported.

What does randomization contribute?

Randomization assigns the treatment sequence by chance, which can reduce systematic allocation differences. In a crossover, the sequence and timing matter because each subject experiences multiple conditions. Randomizing sequence can help distribute period-related influences across conditions. The registry describes randomization of lens order, driving-time sequence, route, and hazard and pedestrian locations. It does not report whether period or carryover effects were tested or how such effects were addressed in the final model.

Masking subjects may reduce the influence of expectations on performance or reporting, but the record only identifies subject masking. It does not say who else was masked or whether masking was assessed. Because driving outcomes include measured performance tasks, the extent to which observers, route staff, or analysts knew the assigned condition cannot be determined from this entry.

What does the noninferiority label mean?

In general, a noninferiority analysis asks whether an intervention is not worse than a comparator by more than a prespecified acceptable margin. The sponsor’s analysis is labeled NON INFERIORITY and reports a model-based estimate and interval. The registry does not state the noninferiority margin, the decision rule, or the rationale for the margin. The label alone is not enough to determine whether the criterion was met or whether the result supports a meaningful conclusion. That assessment requires the margin and the planned analysis details.

The sign of a contrast also depends on the endpoint orientation and the order of comparison. Here, the registry defines positive Z-scores as better performance than the mean, but it does not state the sponsor model’s contrast convention beyond its reported result for the groups. Interpretations should therefore retain the sponsor’s stated group order and avoid treating the sign as a clinical judgment without the complete analysis specification.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated contrast. For the unadjusted Test-versus-Control 1 primary comparison, the estimate is 0.067 and the confidence interval extends from -0.19 to 0.324. The interval includes zero and allows for a negative as well as a positive difference. It is therefore not a narrow estimate centered on a single direction or magnitude. The unadjusted p-value is 0.609, but that value does not indicate the probability that the conditions are the same.

The sponsor’s Linear Mixed Model reports a primary estimate of 0.069 and a 95% confidence interval from -0.045 to 0.183. Its interval also includes zero. The interval is tied to the sponsor model and should not be combined with the unadjusted interval, which was calculated from posted summaries. Since the record does not report the model specification or noninferiority margin, the interval cannot independently establish whether a noninferiority criterion was satisfied.

In general, a wider interval indicates less precision, while a narrower interval indicates more precision under the analysis assumptions. Precision depends on factors including variability, sample information, and the analysis model. The crossover design can use within-subject comparisons, but the registry’s arm summaries do not show the within-subject correlation needed to reproduce that analysis. The record also does not provide confidence intervals for every listed secondary outcome.

These intervals address statistical uncertainty, not clinical importance. The registry does not report a threshold for a meaningful difference on the nighttime driving composite. Consequently, neither the point estimate nor the interval alone identifies which possible differences would matter in practice. Interpretation also depends on the population analyzed: the primary population excludes subjects with a major protocol violation, and the record does not describe the reasons or extent of exclusions.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are planning calculations based on the observed effects, not the trial’s original design assumptions. For these continuous and binary outcomes, the listed figures are participants per arm, not total events. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the stated fraction of the observed effect as the effect to detect. The trial’s own sample-size justification and original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the assumed effect under the planning assumptions, if that effect is real and the assumptions hold. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These are design illustrations for a future study, not results from the completed trial.

The effect-size rows illustrate planning for 100%, 75%, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so more participants are needed to detect it at the same power and significance level. This relationship is a general feature of statistical planning, not a prediction that a future study will observe the same effect or require exactly the illustrated sample size.

These calculations do not account for every feature of a crossover study, and their assumptions specify equal allocation between two arms. They should therefore be treated as simplified planning aids, not as a reconstruction of the study’s design process. This is not observed power; it is a planning illustration based on the observed effect estimate.

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 = 0.067; pooled standard deviation σ = 0.454.
2. n = 2 × (1.96 + 0.842)² × 0.454² / 0.067² = 721.7, rounded up to 722 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 <- 0.067                      # observed difference in means
sigma <- 0.454300808936106                     # 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(3330275)
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 = 722 (80% power), 967 (90% power)
 75% of observed effect: n per arm = 1,284 (80% power), 1,718 (90% power)
 50% of observed effect: n per arm = 2,887 (80% power), 3,865 (90% power)
power.t.test: 722.7 
Simulated power at n = 722 per arm: 0.800 (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 the sponsor’s Test-versus-Control 1 primary analysis as a Linear Mixed Model of final values. The reported mean difference is 0.069, with a 95% confidence interval from -0.045 to 0.183. It is labeled NON INFERIORITY, and no p-value is reported. The noninferiority margin and the full model specification are not reported in the registry record.

The unadjusted recalculation from the posted arm summaries gives a mean difference of 0.067, with an interval from -0.19 to 0.324 and an unadjusted p-value of 0.609. The point estimates are close, but the methods differ: the recalculation uses summary statistics, whereas the sponsor reports a mixed-model analysis in a crossover study. The recalculation does not reproduce the sponsor’s model or its treatment of within-subject data.

The sponsor result is the trial-reported analysis and should be interpreted as such. The recalculation is a transparent, simple comparison of posted summaries, useful for context but not a replacement for the sponsor’s planned analysis. The registry’s noninferiority label cannot be evaluated fully without the margin and decision rule. No discrepancy flag is indicated in the registry record, but that does not remove the distinction between the two analytical approaches.

15. Multiplicity, Missing Data and Analysis Populations

The record lists one primary endpoint and multiple secondary outcomes, with comparisons involving the Test condition and both control conditions. When many outcomes or contrasts are examined, the chance of at least one apparently unusual result can increase even if there are no true differences. In general, multiplicity procedures can limit this risk, but the registry does not report whether an adjustment was planned or used. It also does not report a testing hierarchy, a prespecified ordering of secondary outcomes, or which comparisons were intended to be confirmatory.

The secondary sponsor analyses are labeled NON INFERIORITY or EQUIVALENCE, but the record does not provide the corresponding margins or full decision rules. These labels do not resolve the multiplicity question. Without the statistical plan, it is not possible to determine how the sponsor handled the collection of primary and secondary hypotheses or whether the reported confidence intervals were adjusted for multiple testing.

The primary population is defined as subjects who completed the study without a major protocol violation. The registry does not report the number excluded from that population, reasons for protocol violations, the handling of missing measurements, or whether any imputation was used. It does not describe a sensitivity analysis comparing analysis populations. The detailed population used for each secondary outcome is also not stated in the available record.

These omissions matter because missing or excluded observations can affect estimates, particularly when completion or exclusion is related to performance or treatment condition. The crossover structure makes the pattern of available measurements relevant: a subject may have observations for some conditions but not others. The registry does not describe how incomplete sequences or period-specific missing outcomes were handled. As a result, the available entry cannot establish the robustness of the findings to missing data or deviations from the planned analysis population.

16. 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.

The registry reports zero serious adverse events in each of the Test, Control 1, and Control 2 groups. It also reports zero other adverse events and zero deaths for each group. The reported number at risk is 24 in each condition. These are the adverse-event figures recorded for this study, not a guarantee that no risk exists.

Zero reported events in a study of this size provides limited information about uncommon events or events that might occur with longer exposure. The registry record does not give detailed event narratives, exposure duration for safety assessment, or a separate explanation of how adverse events were collected. The study’s reported endpoint timeframe was 15 Minutes Post Lens Fitting, but that does not establish the full safety-observation period.

The figures should therefore be read as a description of what was recorded in the trial, rather than proof that the devices are free of adverse effects. They also do not support comparisons of rare-event risk between conditions. The registry lists no serious adverse-event terms for further description.

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

The posted results describe nighttime driving and visual performance under the study’s conditions, using an investigational contact lens and two control conditions. For the primary endpoint, the sponsor reports a model-based estimate with a 95% confidence interval that includes zero. The simple unadjusted comparison from arm summaries also has an interval that includes zero. These results do not provide a precise estimate confined to one direction of difference.

That interpretation is not the same as concluding that the conditions perform identically. A failure to establish a clear difference does not establish equivalence, and a confidence interval including zero can still include effects in either direction. The sponsor’s noninferiority label cannot be independently evaluated without the margin and decision rule. Similarly, a statistically non-significant unadjusted p-value is not evidence that there is no effect.

The composite score summarizes six driving measures, but the registry does not state what size of difference would be meaningful to drivers. The score also reflects the selected components and equal weighting chosen for the composite. The available results do not establish how any observed contrast translates into practical driving consequences or whether it applies outside a closed-road circuit.

The trial enrolled 24 and used a crossover design, with the primary analysis population limited to subjects completing the study without a major protocol violation. The registry does not report full eligibility criteria, missing-data handling, details of the model, or the original sample-size rationale. These limitations affect how confidently the estimates can be generalized or reproduced. The safety record lists no adverse events in the reported categories, but the study record does not establish that uncommon or longer-term risks are absent.

Overall, the results should be read as estimates from a specific randomized crossover study, not as general proof for or against a treatment. They provide limited evidence about the measured tasks and conditions; they do not support medical advice or claims about outcomes that were not assessed.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it uses a crossover design for performance outcomes that can be measured repeatedly in the same subjects. In general, within-subject comparisons can account for stable differences between people, while randomized sequence can help distribute period-related influences. The design also randomized driving-time sequence and routes, with hazard and pedestrian positions varied across routes. These features are relevant to reducing systematic differences in the testing conditions.

The composite primary endpoint creates a second statistical issue: it condenses six different measures into one score. Standardizing the component measures makes averaging possible despite their differing units, and equal weighting gives each component the same contribution. That is a clear scoring rule, but the result still depends on the selected measures, their transformations, and the weighting. The registry does not report a threshold for a meaningful difference on the composite.

The comparison of the simple recalculation with the sponsor’s mixed-model result illustrates why an analysis should match the study design. Arm-level means and standard deviations support a basic contrast, but do not retain all information about repeated measurements and within-subject dependence. The sponsor’s model is therefore central to interpreting the trial’s reported analysis, even though the model details are not available in the registry record.

Finally, the record highlights the distinction between a label and an evaluable statistical conclusion. The sponsor’s primary result is labeled noninferiority, and secondary results include equivalence labels, yet the margins and decision rules are not reported. Without them, readers cannot assess the criteria behind those labels. This is a useful reminder that estimates, intervals, analysis assumptions, and prespecified decision boundaries are all needed for a complete 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.

Several limitations specific to this study constrain interpretation. Enrollment was 24, and the registry does not report a justification for the planned sample size or the original design assumptions. The planning illustrations based on observed effects are not evidence that the completed study had adequate precision for its primary question.

The study used a three-period, three-treatment crossover, but the registry does not describe the washout schedule, period effects, possible carryover, or how sequence was represented in the sponsor’s model. The sponsor analysis is identified as a Linear Mixed Model, but the model terms and covariance structure are not reported. The unadjusted calculations from summary statistics cannot account for within-subject correlations.

The primary analysis population excludes subjects with a major protocol violation. The number and reasons for exclusions, missing measurements, and handling of incomplete treatment sequences are not reported. The registry does not provide a detailed account of the analysis populations used for the secondary outcomes or sensitivity analyses.

The record names six secondary outcomes, but numerical result details are not present for all of them. It also does not report the multiplicity strategy or the noninferiority and equivalence margins used in sponsor analyses. The composite endpoint’s clinical-meaning threshold is not reported. Finally, driving was assessed on a closed-road circuit under study conditions, so the record alone cannot establish generalizability to other settings or real-world driving.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluating the Impact of JJVC Senofilcon A - Based Contact Lens With New UV-blocker on Day and Night Driving Performance — NCT03330275.
• Registry record last updated 2018-08-07; status last verified 2018-07.
• Results first posted 2018-08-07.
• 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

NCT03330275 is a completed Phase 2 randomized, single-masked crossover study sponsored by Johnson & Johnson Vision Care, Inc. It evaluated an investigational senofilcon A-based contact lens with a new UV-blocker against two control conditions during daytime and nighttime closed-road driving tasks. Enrollment was 24.

The primary outcome was the overall nighttime driving Z-score, a composite of six measures, reported 15 Minutes Post Lens Fitting. The sponsor reported a Linear Mixed Model comparison of Test with Control 1, labeled NON INFERIORITY. The posted unadjusted comparison from summary statistics has a mean difference of 0.067 and a confidence interval from -0.19 to 0.324. The record does not report the noninferiority margin or full model details.

The registry lists multiple secondary outcomes and reports no serious adverse events, other adverse events, or deaths in the listed groups. Multiplicity handling, missing-data methods, and the original sample-size justification are not reported in the registry record.