Driving Simulator Study Comparing Two Modes of Presbyopic Correction With Contact Lenses: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Driving Simulator Study Comparing Two Modes of Presbyopic Correction With Contact Lenses (NCT02189863), a randomized na study. The primary outcome is Driving Reaction Time to Hazards (as Measured by Time to Brake, in Seconds).

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, crossover study of contact-lens correction modes for presbyopia. The stated objective was to compare the effect of multifocal and monovision soft contact lenses on simulated driving performance in mid-late presbyopes. The registry lists 33 participants as enrolled and marks the study completed. Its phase is recorded as not applicable.

The primary comparison involved lotrafilcon B monovision lenses, AOAMV, and lotrafilcon B multifocal lenses, AOAMF. The two sequence descriptions indicate that participants wore one lens mode for 2 weeks in Period 1 and the other for 2 weeks in Period 2. One sequence began with AOAMV and then used AOAMF; the other began with AOAMF and then used AOAMV. The crossover design exposes participants in each sequence to both correction modes, while the sequence assignment determines the order of exposure.

The primary outcome was assessed at Week 2 of each period. The registry says that one eye, designated the study eye, contributed to the analysis. The primary population was per-protocol: randomized participants assigned to their groups who completed both lens follow-up evaluations without a documented protocol deviation that impacted assessment of the hypotheses. The posted primary summaries list 21 observations for each mode. The record does not explain the relationship between those analysis counts and the total enrollment, or detail how the crossover pairing and period or sequence effects were handled statistically.

Other devices and conditions appear in the intervention and safety listings, including single-vision contact lenses and habitual contact lenses. The posted primary contrast, however, is AOAMF versus AOAMV. The registry does not report the original design assumptions, the trial’s sample-size justification, or further masking procedures beyond the single-masked designation.

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: Of the 33 enrolled, 6 participants were exited as screen failures prior to randomization. This reporting group includes all randomized participants who successfully tried at least one study lens (27).

First 2 Weeks

Reasons for not completing this period:

Second 2 Weeks

Analysis population for the primary outcome, as defined in the registry: This analysis population includes all randomized subjects in the groups to which they were randomly assigned who successfully completed both study lens follow-up evaluations without a protocol deviation that was documented as impacting the assessment of the hypotheses (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.

Population: This analysis population includes all randomized participants who successfully tried at least one study lens.

6. Primary Endpoint

The registry lists the primary outcome as Driving Reaction Time to Hazards (as Measured by Time to Brake, in Seconds), measured over Week 2, each period.

The primary endpoint was driving reaction time to hazards during simulated night-time driving, measured as the time to brake in seconds. It was assessed at Week 2 of each study period. The registry specifies that one eye, the study eye, contributed to the analysis and that the measure was prespecified for the AOAMV and AOAMF conditions.

Reaction time is a continuous measure: each observation can take a range of numerical values rather than falling into a small set of categories. Reporting a mean gives a summary of the observed braking times, while the standard deviation describes how dispersed those times were within each lens condition. The posted means were 1.89 seconds for AOAMV and 1.88 seconds for AOAMF. The posted comparison estimates the mean difference, AOAMF relative to AOAMV, as -0.01 seconds.

In general, a simulator endpoint offers a standardized way to assess a specific performance measure under controlled driving conditions. It is not the same as measuring driving in ordinary traffic or establishing how a difference would affect real-world safety. The registry record does not report a threshold for a clinically or practically important difference in braking time, nor does it explain how the simulator measure was validated for that purpose. The endpoint therefore describes a measured aspect of simulated performance, not a complete account of driving ability or safety.

7. Results Posted in the Registry

• AOAMF: mean 1.88 versus 1.89 on control; difference -0.01 (95% CI -0.13 to 0.11), standardized effect d = -0.05; z-test p = 0.875.

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.

Standard Deviation of Lateral Positioning

• 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:
  • AOAMF: mean 0.35 versus 0.35 on control; difference 0.00 (95% CI -0.03 to 0.03), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AOAMF and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: standard deviation of lateral positioning, measured in meters at Week 2 of each period. The summary pattern is that the reported means are the same in the two lens conditions. The comparison is accompanied by an unadjusted p-value of 1.0. As with the primary endpoint, these figures describe the analyzed sample and do not establish that the underlying conditions are identical.

This outcome concerns variability in lateral position during the simulator task, whereas the primary outcome concerns time to brake in response to hazards. It is therefore a related but distinct measure of simulated driving performance. The secondary result does not contradict the primary result: both posted comparisons are consistent with little apparent separation in their sample means, but they address different features of the simulator assessment and carry their own uncertainty.

In general, secondary outcomes can add context by showing whether a pattern is limited to one measure or appears across different measures. They are often less decisive than a prespecified primary outcome, especially when the registry does not describe a multiplicity strategy. If several outcomes or comparisons are tested, an unadjusted p-value does not account for the full set of tests. The registry lists the secondary endpoint but reports no analyses in its reported-analyses field, and it does not give a broader statistical analysis plan.

The secondary result should consequently be read as descriptive and supportive, not as independent confirmation of a treatment effect or of equivalence. Its relationship to the primary result is qualitative: both summaries show closely aligned reported means in this analyzed sample. Neither result establishes how the measures would behave in other driving contexts, and neither supplies a threshold for deciding whether a particular difference matters in practice.

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

• Standard Deviation of Lateral Positioning

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry summarizes it using a mean and standard deviation for each lens mode. In general, a mean locates the center of a set of measurements. A standard deviation describes how spread out individual measurements are around that center. These summaries make the overall levels and variability visible, but do not show the full distribution of observations or how individual participants’ results changed between periods.

The registry reports means of 1.89 seconds for AOAMV and 1.88 seconds for AOAMF. It reports standard deviations of 0.22 and 0.19 seconds, respectively. The comparison is expressed as a mean difference of -0.01 seconds, with AOAMF as the comparison condition against AOAMV. In plain language, the negative sign indicates that the posted mean for AOAMF was lower than the posted mean for AOAMV. The difference is an estimate from the analyzed participants, not a guaranteed difference in other populations or settings.

In general, a confidence interval describes a range of values reasonably compatible with the data and the analysis assumptions. It communicates uncertainty in an estimate rather than only reporting a single point estimate. For this comparison, the posted interval crosses zero, so the results are compatible with no mean difference and with nonzero differences in either direction. An interval’s usefulness depends on the analysis being appropriate for the study design. The registry does not describe the model used to construct this interval.

The reported p-value is 0.875 and is marked unadjusted. In general, a p-value assesses how surprising data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor a measure of the size or practical importance of a difference. A large p-value does not establish equivalence. Equivalence or non-inferiority questions require prespecified margins and appropriate analyses; those are not reported in the registry record.

The crossover design is statistically relevant. In a crossover study, the same participant receives different conditions in different periods, so observations from that participant may be related. In general, accounting for this pairing can improve precision when the analysis appropriately models within-participant relationships. Period effects and order or sequence effects can also matter, as can any carryover from one condition into the next. The registry gives the two treatment sequences and two-week periods, but does not report the statistical model, whether period or sequence terms were included, how pairing was handled, or whether carryover was assessed. It is therefore not possible to infer those methods from the posted summary alone.

The primary population is described as per-protocol. It includes randomized subjects assigned to their randomized groups who completed both study-lens follow-up evaluations without a documented protocol deviation that impacted assessment of the hypotheses. In general, a per-protocol analysis focuses on participants who met specified adherence and assessment criteria. It can differ from an analysis of all randomized participants and may be affected by exclusions after randomization. The record does not report participant-level exclusions, reasons for missing assessments, or the number randomized to each sequence. It also does not report an intention-to-treat analysis.

The registry identifies the study as single-masked but does not say who was masked or how masking was maintained. It does not report prespecified handling of missing data, imputation methods, model diagnostics, or adjustments for any covariates. Those omissions limit assessment of how the reported uncertainty reflects the crossover structure and the analysis population. General statistical principles can explain why such details matter, but they do not establish which methods were used in this study.

The comparison is accompanied by an unadjusted p-value. In general, when many outcomes or contrasts are examined, the chance of at least one apparently notable result can increase unless multiplicity is addressed. The registry lists a primary outcome and a secondary outcome, but does not report a multiplicity strategy or full analysis plan. The primary result should therefore be distinguished from the secondary result, and the secondary finding should be interpreted cautiously rather than treated as a separate confirmatory conclusion.

Finally, the registry reports an observed estimate and a planning illustration based on that observed effect. These are different uses of statistics. The observed summaries describe this analyzed sample. The planning illustration shows how participant requirements would vary under stated assumptions for future planning; it does not describe the trial’s original design, and it is not a measure of power achieved by the completed trial.

11. Confidence Intervals and Precision

The estimated primary mean difference was -0.01 seconds for AOAMF relative to AOAMV. The registry’s confidence interval for that estimate spans values on both sides of zero. This means the posted data do not pin down the direction of a possible underlying difference with certainty: the interval includes no difference as well as effects in either direction. The interval communicates more than the point estimate alone, because it indicates the range of values compatible with the analysis and its assumptions.

In general, narrower confidence intervals indicate greater precision, while wider intervals indicate more uncertainty about the estimated quantity. Precision depends on factors such as the amount of information in the data, variation in the measured outcome, and the analysis used. The standard deviations were 0.22 seconds for AOAMV and 0.19 seconds for AOAMF, and the posted summaries list 21 observations per condition. Those figures describe the analyzed summaries but do not by themselves reveal whether the crossover pairing was used effectively.

Because the registry does not report a clinically or practically important threshold for reaction time, the interval cannot be classified against such a threshold. It is not enough to observe that the means are close or that the interval crosses zero to conclude that meaningful differences have been ruled out. Establishing equivalence would require a prespecified margin and a suitable analysis, neither of which is reported in the registry record.

Precision also depends on whether the analysis matches the design. The study used two periods and two sequences, but the registry does not explain how within-participant correlation, period effects, sequence effects, or possible carryover were handled. The confidence interval should therefore be read as the interval reported for the posted comparison, without assuming an unreported statistical model or additional design adjustment.

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 illustration gives participants per arm for 80% power and participants per arm for 90% power. These are not total event counts: the registry’s planning assumptions specify participants per arm for non-time-to-event outcomes, and this is a continuous outcome. The illustration uses equal allocation between the two arms, a two-sided significance level of 0.05, and a normal approximation. Its target effect is set at the stated fraction of the observed effect.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For each assumed effect, the 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting an effect of that size under the stated assumptions. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are hypothetical planning scenarios, not the number enrolled in this completed study.

The figures rise as the assumed effect becomes smaller: an effect that is harder to distinguish from random variation generally requires more participants for the same target power. This illustration starts from the observed effect, so it is particularly sensitive to the estimate from this small analyzed sample. It should not be taken as the original design justification; the trial’s original sample-size assumptions are not reported in the registry record. The illustration is not observed power.

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 = -0.010; pooled standard deviation σ = 0.206.
2. n = 2 × (1.96 + 0.842)² × 0.206² / -0.010² = 6,632.3, rounded up to 6,633 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 <- -0.01                      # observed difference in means
sigma <- 0.205548047910945                     # 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(2189863)
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 = 6,633 (80% power), 8,879 (90% power)
 75% of observed effect: n per arm = 11,791 (80% power), 15,785 (90% power)
 50% of observed effect: n per arm = 26,530 (80% power), 35,516 (90% power)
power.t.test: 6633.3 
Simulated power at n = 6,633 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 identifies one primary outcome and one secondary outcome, but it does not report a multiplicity adjustment or a plan for interpreting multiple tests. The primary comparison has an unadjusted p-value, and the secondary comparison also has an unadjusted p-value. In general, when more than one hypothesis is tested, the chance of obtaining at least one small p-value by chance can rise. A prespecified multiplicity approach can help control that issue. Without a reported plan, the secondary result should be treated as exploratory or supportive rather than as a separate confirmatory claim.

The record does not report an analysis plan detailing the order of hypotheses, any planned subgroup analyses, or which outcomes were intended to receive formal statistical testing beyond the registry’s identification of the primary measure. It also does not report interim analyses or stopping rules. Their absence from the record does not establish that they did or did not occur; such details are not reported in the registry record.

Missing-data information is limited. The primary analysis population requires successful completion of both study-lens follow-up evaluations and excludes documented protocol deviations considered to affect assessment of the hypotheses. The registry reports enrollment of 33 and 21 observations in each primary condition, but does not provide a participant flow, reasons for non-completion, reasons for exclusion, or details of missing measurements. It does not report an imputation method or sensitivity analyses for missing data.

The record describes the primary analysis as per-protocol and does not report an intention-to-treat result. In general, different analysis populations answer somewhat different questions. Excluding participants after randomization can affect how representative the analyzed group is of those assigned, particularly if exclusions relate to outcomes or treatment experience. The registry’s information is not sufficient to assess whether that concern arose in this study.

Because the study is a crossover, reporting of the analytical population and missingness by period and sequence would also help readers understand which paired observations contributed to the estimate. Those details, along with methods for handling period, sequence, and within-participant dependence, are not reported in the registry record.

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.

Most frequent non-serious adverse event terms

The registry lists serious adverse events for five groups: AOAMV, AOAMF, Lotra B SVD, Biofinity MF, and Habitual. It reports zero serious adverse events in each listed group. The numbers at risk were 25 for AOAMV, 23 for AOAMF, 23 for Lotra B SVD, 21 for Biofinity MF, and 27 for Habitual. These safety denominators are not the same as the 21 observations reported for each primary outcome condition, so they should not be substituted for the primary analysis counts.

In general, a zero count in a study group means that no events of that category were recorded among the participants at risk in that group during the reported study period. It does not establish that an event is impossible or that the risk is zero in a broader population. The record does not provide a detailed description of serious-event definitions or exposure time for these groups.

Death counts are not reported in the registry record. The registry also lists other adverse events separately, but those are not serious adverse events. Safety counts from this study should be read as descriptive registry data, not as a comprehensive comparison of all possible harms.

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

The results show that the mean simulated night-driving time to brake was very similar in the analyzed AOAMV and AOAMF conditions: 1.89 seconds and 1.88 seconds, respectively. The estimated mean difference was -0.01 seconds for AOAMF relative to AOAMV, and the reported unadjusted p-value was 0.875. The confidence interval crosses zero, so the posted comparison does not identify a clear difference in the population mean under the reported analysis.

That interpretation is not the same as concluding that the two modes are equivalent. A failure to identify a difference can reflect a genuinely small difference, uncertainty in the estimate, or limitations in the design or analysis. Equivalence requires a clinically or practically justified margin and a suitable prespecified analysis. No such margin is reported in the registry record. The posted estimate and interval cannot, on their own, rule out every difference that could matter.

The outcome is a simulator measure of braking time during simulated night driving. It does not directly report real-world driving performance, collision risk, or overall visual function. The study’s conclusion should be kept within the measured setting and population. The registry does not report a threshold connecting a change in time to brake with practical driving consequences.

The analysis population was per-protocol, and the registry does not explain why the outcome summaries include 21 participants per condition when enrollment was 33. It also does not report enough statistical detail to establish how the crossover design was modeled. These limitations affect how confidently the estimates can be generalized or interpreted as a complete account of the randomized comparison.

Accordingly, the posted data describe a close pair of sample means and substantial uncertainty about the exact underlying difference. They do not establish that one correction mode is better, that the modes are interchangeable, or that either mode is appropriate for an individual. The findings are statistical evidence about the specified endpoint, rather than medical advice or a complete assessment of driving safety.

17. Why This Trial Matters Statistically

This trial illustrates several important statistical features of clinical research. First, its crossover design makes within-participant comparisons potentially informative, but also makes the analysis method important. Measurements from the same participant are generally related, and period, sequence, or carryover effects may influence the comparison. A registry summary that gives group means and a mean difference without describing those modeling choices leaves a meaningful part of the statistical interpretation unresolved.

Second, a result that is not statistically significant is not proof of equivalence. The primary means are close and the p-value is large, but equivalence is a distinct question that requires a prespecified margin and an analysis designed to evaluate that margin. Neither is reported in the registry record. This distinction is essential when interpreting comparisons that appear numerically similar.

Third, estimates and confidence intervals should be considered together. A point estimate gives one best summary of the observed contrast, while the interval expresses uncertainty around it. Without a reported threshold for a meaningful change in braking time, readers cannot translate the interval into a judgment about practical importance.

Finally, sample-size planning illustrations based on an observed effect are not the same as a trial’s original design calculation or its achieved power. The illustration can show how planning requirements change under different assumptions, but it does not explain why this study enrolled its particular number of participants. The trial’s original sample-size justification is not reported.

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 record leaves several trial-specific uncertainties. Although 33 participants were enrolled, the primary outcome summaries list 21 participants in each condition, and the record does not provide a flow diagram, sequence-specific counts, or reasons for exclusion or non-completion. The per-protocol definition requires completion of both follow-up evaluations and excludes certain documented deviations, but the actual application of those criteria is not described.

The design is identified as randomized, single-masked, and crossover, and the two sequences are described. However, the record does not report who was masked, the statistical model, or how the analysis accounted for paired measurements, period effects, sequence effects, or possible carryover. These are particularly relevant to interpreting a crossover comparison and its confidence interval.

The endpoint is a simulator measure, and no threshold for a practically important change in time to brake is reported. The record does not establish how the measured difference relates to real-world driving outcomes. Generalizability beyond the stated presbyopic population, simulated night-driving task, and study conditions is therefore uncertain.

The registry does not report the trial’s original sample-size justification, a full statistical analysis plan, multiplicity procedures, interim analyses, missing-data methods, or sensitivity analyses. The results should be interpreted as the posted summaries rather than as a fully documented analysis of every potential source of uncertainty. Safety counts are also descriptive, with death counts not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Driving Simulator Study Comparing Two Modes of Presbyopic Correction With Contact Lenses — NCT02189863.
• Registry record last updated 2016-02-18; status last verified 2016-01.
• Results first posted 2016-01-20.
• 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 record describes a completed randomized, single-masked crossover study sponsored by Alcon Research, with 33 participants enrolled. Its stated objective was to compare multifocal and monovision soft contact lenses in mid-late presbyopes using simulated driving performance.

The primary endpoint was time to brake in response to hazards during simulated night driving, assessed at Week 2 of each period. In the per-protocol summaries, the mean was 1.89 seconds for AOAMV and 1.88 seconds for AOAMF. The estimated mean difference was -0.01 seconds, with an unadjusted p-value of 0.875. The secondary outcome was standard deviation of lateral positioning.

The record gives the crossover sequences and the primary population definition, but does not report the detailed statistical model, the original sample-size justification, missing-data methods, or a multiplicity plan. The findings should therefore be read as estimates for the specified simulator outcomes, with uncertainty and reporting limitations.