Bifocal Lenses In Nearsighted Kids: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bifocal Lenses In Nearsighted Kids (NCT02255474), a randomized na study. The primary outcome is Refractive Error Progression.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-masked, parallel trial of soft contact lenses in children ages 7 to 11 years old. The interventions were Biofinity Multifocal D lenses with +1.50 D and +2.50 D adds, alongside Biofinity soft spherical contact lenses as the control. The study status is completed. The record lists enrollment as 294 and gives the study start as 2014-09-22 and primary completion as 2019-06-24. These registry fields describe the study record; they do not establish that every enrolled participant contributed to every posted outcome analysis.

The primary outcome was refractive error progression over 3 years, measured by cycloplegic autorefraction in both eyes and intended to be assessed yearly. The outcome summary reports arm means and standard deviations, and the posted comparison statistics are mean differences. The registry also identifies outcomes concerning ocular shape change and eye growth, peripheral defocus and myopic progression, and axial length progression. Three secondary outcomes have posted results.

The phase is listed as NA. The sponsor is Ohio State University. The record labels allocation randomized, masking triple, and the model parallel. It does not specify which individuals or roles were masked, how randomization was generated or implemented, or how allocation concealment was handled. The original sample-size justification, detailed analysis plan, and the rules for including participants in each analysis are not reported in the registry record. Those absences limit how fully the design and analysis can be evaluated from the registry 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.

Overall Study

Reasons for not completing this period:

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 Refractive Error Progression, measured over 3 years.

The primary endpoint is refractive error progression, expressed in diopters, over 3 years. The registry describes measurement by cycloplegic autorefraction in both eyes, with yearly assessments intended to track change in nearsightedness. The posted endpoint summaries are means with standard deviations. A mean describes the central value of a continuous measurement, while the standard deviation describes how spread out individual measurements are around that mean.

Repeated assessment is relevant because the endpoint concerns change over time, rather than a single observation alone. The outcome description says measurements would be made yearly, but the posted arm summaries are presented as final values and do not, by themselves, show the full course of measurements or each participant’s trajectory. The registry’s reported primary analysis is identified as a mixed models analysis of mean difference in final values. Its listed result is not accompanied by a confidence interval or a description of the specific model terms.

Refractive error is the direct measure named in the primary outcome. The secondary outcomes include eye growth and axial length, which describe related but distinct aspects of the study question. Their results should not be treated as interchangeable with the primary endpoint. The registry record does not report how the two eyes were handled statistically or whether yearly observations were analyzed in a particular repeated-measures structure.

7. Results Posted in the Registry

• Biofinity +1.50 D Add: mean -3.32 versus -3.46 on control; difference 0.14 (95% CI -0.24 to 0.52), standardized effect d = 0.10; z-test p = 0.468.
• Biofinity +2.50 D Add: mean -2.84 versus -3.46 on control; difference 0.62 (95% CI 0.28 to 0.96), standardized effect d = 0.51; z-test p = <0.001.

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.

Association of Peripheral Defocus to Myopic Progression

• 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:
  • Biofinity +1.50 D Add: mean -0.85 versus -1.01 on control; difference 0.16 (95% CI -0.05 to 0.37), standardized effect d = 0.21; z-test p = 0.133.
  • Biofinity +2.50 D Add: mean -0.56 versus -1.01 on control; difference 0.45 (95% CI 0.26 to 0.64), standardized effect d = 0.68; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biofinity +1.50 D Add and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Biofinity +2.50 D Add than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Axial Length Progression

• 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:
  • Biofinity +1.50 D Add: mean 25.12 versus 25.08 on control; difference 0.04 (95% CI -0.22 to 0.30), standardized effect d = 0.04; z-test p = 0.759.
  • Biofinity +2.50 D Add: mean 24.81 versus 25.08 on control; difference -0.27 (95% CI -0.51 to -0.03), standardized effect d = -0.32; z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biofinity +1.50 D Add and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Biofinity +2.50 D Add than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address related but different questions: peripheral defocus in relation to myopic progression, axial length progression, and ocular shape change and eye growth. The posted results include analyses for peripheral defocus and axial length, while the registry identifies three secondary outcomes. Taken together, these measures broaden the picture beyond the primary refractive error endpoint, but they do not measure the same construct and need not move in identical ways.

The posted comparisons show that patterns across the secondary measures are not uniform across both bifocal add groups. Some comparisons have intervals that include zero, while others do not. This means the secondary results should be considered as a collection of exploratory evidence rather than as one consistent, definitive confirmation of the primary result. The outcomes may provide useful context about related optical or eye-growth measurements, but they do not independently settle the primary question.

Unadjusted secondary p-values carry less weight because multiple outcomes and group comparisons create more opportunities for apparently notable results to arise by chance. The registry record does not report whether multiplicity was addressed in the sponsor’s analysis or how the secondary outcomes were prioritized. Without that information, a nominal p-value should not be treated as a confirmatory finding. Secondary estimates and their uncertainty can still inform future research questions, while claims about a coherent pattern require caution and a prespecified analysis framework that is not available in the registry record.

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

• Ocular Shape Change and Eye Growth
• Association of Peripheral Defocus to Myopic Progression
• Axial Length Progression

9. Statistical Interpretation

10. Statistical Methods Explained

The primary arm summaries describe a continuous outcome. For such an outcome, a mean gives the average measurement in the analyzed group, and a standard deviation gives a sense of variation among observations. The reported means are negative values because refractive error is recorded on a scale where these values represent nearsightedness; the statistical comparisons concern differences between group summaries. The registry does not provide an individual-level dataset, so the re-calculations use only the posted group means, standard deviations, and analysis counts.

What does a mean difference express?

A mean difference expresses the contrast between the average outcome in one group and the average in the comparator group. The re-calculated comparisons are unadjusted: they do not account for covariates or any other model features. The sign indicates which group’s posted mean is higher on the measurement scale. Interpreting that sign in clinical terms requires attention to the outcome’s scale and how it is defined; a numerical difference alone does not establish practical importance.

The two re-calculations use Biofinity as the comparator, one at a time. The arm-level summaries allow these direct contrasts, but they do not reproduce a longitudinal analysis of yearly observations. The registry labels its own primary result as a mixed models analysis of mean difference in final values. A mixed model can, in general, represent relationships among repeated measurements or account for modeled sources of variation. The registry record does not report the model specification, covariance structure, adjustment variables, or which observations were used. It would therefore be inappropriate to assert exactly how the sponsor’s model handled repeated measures or missing observations.

Why do the confidence intervals matter?

A confidence interval gives a range of estimates compatible with the data and the method used, subject to the method’s assumptions. A narrower interval indicates greater statistical precision than a wider interval, but precision is not the same as absence of bias or clinical importance. For a mean difference, an interval that includes zero remains compatible with no difference on the measured scale as well as with values on either side of zero. An interval excluding zero indicates that zero is not within that calculated range; it does not establish causation on its own or substitute for the trial’s prespecified analysis.

The p-values accompanying the re-calculations are unadjusted. They relate to individual comparisons and do not account for the fact that several groups and outcomes appear in the registry. They should not be read as a complete family-wise assessment of all questions asked in the trial. Whether the sponsor planned a multiplicity procedure is not reported in the registry record.

What does over-dispersion mean in general?

In general, over-dispersion means that observed variability is greater than a model assumes. When a model underestimates variability, standard errors can be too small, confidence intervals too narrow, and p-values too optimistic. That concern is especially relevant when an outcome or model has a distributional structure that may not match the assumed model. The primary endpoint is continuous and is summarized with means and standard deviations; the registry record does not report an over-dispersion assessment. This general concept should not be taken to mean over-dispersion occurred in this trial.

What can the re-calculations establish?

They provide transparent, simple comparisons based on the posted summaries. They are useful for seeing the direction and uncertainty of the two arm contrasts using one common, unadjusted approach. They cannot establish whether the reported mixed model was correctly specified, reproduce its result, adjust for baseline characteristics, account for within-child or within-eye dependence, or determine how missing data were handled. Nor can they answer questions about the trial’s original hypotheses or analysis decisions, which are not described in enough detail in the registry record.

The posted planning illustrations use an observed effect as a starting point and show hypothetical participant requirements under stated assumptions. They are not evidence about the power the completed study actually had. More detail on those planning assumptions and how to read the resulting figures is given in the sample-size interpretation.

11. Confidence Intervals and Precision

For the primary +1.50 D comparison, the re-calculated mean difference is 0.14, and its 95% confidence interval runs from -0.238 to 0.518. The interval includes zero and extends to values on either side of it. This indicates that the posted summaries do not pin down the direction of this unadjusted contrast precisely. The associated p-value is 0.468.

For the primary +2.50 D comparison, the re-calculated mean difference is 0.62, with a 95% confidence interval from 0.280 to 0.961. This interval lies above zero, so the summary-statistic calculation places the mean contrast in the positive direction across the interval. Its p-value is <0.001. The precision differs between the two comparisons, and the interval is the more informative way to convey the range of estimates compatible with each calculation than a p-value alone.

These intervals are derived from posted summary statistics, not the registry’s mixed models analysis. The registry does not report a confidence interval for its primary analysis result, so the precision of that sponsor-reported estimate cannot be assessed from the record. The confidence intervals also do not incorporate possible uncertainty from unreported analysis choices, missing data, or multiplicity. They quantify sampling uncertainty under the particular re-calculation, not every source of uncertainty surrounding the trial.

Statistical precision and clinical importance are separate considerations. The registry does not state a threshold for a clinically meaningful difference in refractive error, and no such threshold should be inferred from whether an interval includes zero. The interval describes uncertainty in a group-level contrast; it does not describe the likely outcome for a particular child.

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 figures are planning illustrations expressed as participants per arm, not total event counts. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column indicates the hypothetical participants per arm under these assumptions for a design with an 80% probability of detecting the specified effect if that effect is the true one and the model assumptions hold. The 90% power column gives the corresponding hypothetical count for a design with a 90% probability under the same general conditions. These figures are planning targets, not observed characteristics of the completed trial. This is not observed power.

Rows planning for 100% of the observed effect use the full observed effect as the target; rows planning for 75% or 50% use smaller targets. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the stated assumptions. The listed counts are illustrations based on each observed comparison, not a recommendation or a reconstruction of the trial’s original enrollment plan.

The curves should be read as visual versions of the same planning relationship: required participants per arm depend on the effect size being targeted and the selected power level. A curve does not show how many participants were actually analyzed, nor does it establish that a future study will achieve the displayed power. Differences in outcome definition, analysis method, allocation, or other design features could change the requirements.

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 = 0.140; pooled standard deviation σ = 1.348.
2. n = 2 × (1.96 + 0.842)² × 1.348² / 0.140² = 1,455.4, rounded up to 1,456 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 <- 0.14                      # observed difference in means
sigma <- 1.34801485208835                     # 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(2255474)
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 = 1,456 (80% power), 1,949 (90% power)
 75% of observed effect: n per arm = 2,588 (80% power), 3,464 (90% power)
 50% of observed effect: n per arm = 5,822 (80% power), 7,794 (90% power)
power.t.test: 1456.3 
Simulated power at n = 1,456 per arm: 0.797 (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’s own primary analysis is listed as a mixed models analysis across the three groups, with a mean difference in final values of -1.01 and p <0.01. The record does not give a confidence interval for this result or enough model detail to identify precisely how it relates to the arm-specific comparisons. The re-calculations instead compare each bifocal arm with Biofinity using posted means, standard deviations, and analysis counts.

Those approaches yield different reported estimates, and the discrepancy flag indicates that they should not be presented as interchangeable. The sponsor’s own analysis takes precedence over the simple unadjusted re-calculations. The re-calculations remain useful as a transparent check of what the posted summary statistics imply, but they do not override the registry’s reported analysis or show that its model is wrong.

The registry labels the sponsor analysis as a superiority analysis, but that label does not supply missing details about its hypothesis, model, or interpretation. Without a confidence interval or fuller analysis description, the precision and exact estimand of the sponsor-reported result cannot be independently evaluated from the registry record. The two sources of statistics should therefore remain clearly distinguished.

15. Multiplicity, Missing Data and Analysis Populations

The record includes a primary outcome, multiple secondary outcomes, three treatment groups, and several pairwise comparisons. When many comparisons are examined, the chance of at least one apparently unusual result can increase even if no underlying group differences exist. Statistical procedures for multiplicity can address that issue, but the registry record does not report whether the sponsor adjusted for multiple comparisons, which comparisons were considered primary within each outcome, or what testing hierarchy was used.

The p-values attached to the summary-statistic comparisons are explicitly unadjusted. They therefore describe individual comparisons under their calculation assumptions and should not be interpreted as controlling the overall false-positive risk across the full set of outcomes and contrasts. The sponsor’s analysis results are reported separately, but the record does not state how multiplicity was considered in those analyses. The absence of this information does not prove that no plan existed; it means the plan is not reported in the registry record.

Missing-data handling is also not described in sufficient detail. The record gives enrollment and outcome analysis counts, but does not explain why counts differ across registry measures, whether observations were missing, or how any missing observations were addressed. It does not report whether the analysis used all randomized participants, a modified population, or another analysis set. These details matter because results can depend on which observations are included and on assumptions about missingness.

The registry names a mixed models analysis for the primary outcome and for axial length, and a linear regression for a secondary outcome. It does not provide enough information to assess the model assumptions, covariate adjustment, repeated-measure structure, or sensitivity analyses. The specific analysis population and the handling of both eyes are also not reported in the registry record. These omissions limit independent assessment of how robust the reported findings are to analysis choices.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events among 98 participants at risk in the Biofinity group, zero among 98 at risk in the Biofinity +1.50 D Add group, and zero among 98 at risk in the Biofinity +2.50 D Add group. It also reports zero deaths in each group. No top serious adverse event terms are listed.

These figures describe what was posted for the registry’s serious adverse event fields. They do not establish that no adverse experiences of any kind occurred. The record separately lists other adverse events affecting 72 of 97 at risk in the Biofinity group, 71 of 98 at risk in the +1.50 D group, and 75 of 97 at risk in the +2.50 D group. Those other-event figures should not be conflated with serious events.

Safety counts are descriptive and depend on the registry’s definitions, reporting period, and ascertainment. The record does not provide enough detail to evaluate event types, timing, severity beyond the serious-event classification, or relationships to the lenses. Zero reported serious events is not proof that a treatment is free from risk.

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

The posted results describe group-level measurements in a randomized trial comparing two bifocal contact lens add powers with a soft spherical contact lens. The arm summaries and unadjusted re-calculations indicate different levels of evidence for the two primary pairwise contrasts: the +1.50 D comparison has a confidence interval that includes zero, while the +2.50 D comparison has an interval above zero. The registry’s own primary analysis reports a separate mixed-model result, and its estimate differs from the simple re-calculations. Because of that discrepancy, the sponsor’s analysis takes precedence.

These statistics do not, on their own, show what any individual child’s refractive error will be. Group averages can conceal variation among participants, and the standard deviations indicate that measurements were spread within each arm. A statistically distinguishable mean contrast is not automatically important to patients, families, or clinicians; the registry record does not state a threshold for clinical importance.

The findings also do not establish effects beyond the reported 3-year timeframe, explain the mechanism behind any group differences, or demonstrate that results apply to children outside the ages and study context described. Secondary measures offer related information but are not substitutes for the primary endpoint, and unadjusted secondary findings warrant particular caution.

In general, a clinical trial result is one piece of evidence whose interpretation depends on its design, conduct, analysis, precision, and relevance to the question of interest. The registry record leaves several of those details unreported, including multiplicity handling, missing-data methods, and the exact model specification. The statistical summaries can support careful description of the posted comparisons, but they do not constitute medical advice or a standalone basis for individual treatment decisions.

18. Why This Trial Matters Statistically

This trial illustrates why a registry’s own analysis and a simple re-calculation from posted summaries should be kept distinct. The summaries permit direct, transparent arm comparisons, but they do not reproduce a mixed models analysis. When the two sets of estimates differ, as they do in this record, readers need to know which result comes from the trial’s reported analysis and which is an unadjusted calculation. That distinction is central to responsible interpretation.

It also shows why effect estimates and confidence intervals add information beyond p-values. The intervals communicate the range of values compatible with the calculation and help distinguish a less precise comparison from one whose interval lies on one side of zero. Neither an interval nor a p-value answers whether a difference is meaningful in practice, which requires context not specified in the registry record.

The secondary outcomes demonstrate the importance of multiplicity and outcome hierarchy. Several related measures and contrasts can yield a varied pattern, and unadjusted results do not carry the same weight as a prespecified confirmatory analysis. A careful reader can recognize potentially informative secondary signals without treating every nominal finding as conclusive.

Finally, the record makes clear that sample-size planning illustrations are not a substitute for the original protocol’s rationale or an account of the completed study’s power. The assumptions behind hypothetical planning calculations can be stated, while the trial’s own design assumptions remain unreported. Keeping those evidence sources separate helps prevent over-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.

The registry record does not report the detailed randomization procedure, allocation concealment, or which participants and study personnel were masked. Although the trial is labeled randomized and triple-masked, the meaning of that masking label is not elaborated. The record also does not state the original sample-size justification, the planned statistical analysis in full, or whether interim analyses occurred.

The primary outcome description refers to yearly measurements in both eyes, but the record does not explain how eye-level data were combined or modeled. The reported analysis is identified as a mixed models analysis of final values, without model terms, assumptions, or a confidence interval. The simple re-calculations use posted arm summaries and are unadjusted; they cannot resolve the discrepancy with the sponsor’s reported result.

Analysis populations and missing-data methods are not reported in enough detail to explain the counts used for each outcome or to assess sensitivity to missing observations. Multiplicity procedures for the several outcomes and comparisons are also not reported. These gaps constrain interpretation of nominal p-values, especially for secondary outcomes.

The registry’s secondary outcome listing and posted analyses do not provide a complete account of all methods or outcome definitions. The record does not establish a clinically meaningful difference threshold, describe the practical importance of the measured contrasts, or provide enough information to judge generalizability beyond the stated age range and study context. These are limitations of what can be concluded from the registry record, not proof that the underlying trial did not address them elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Bifocal Lenses In Nearsighted Kids — NCT02255474.
• Registry record last updated 2021-03-10; status last verified 2021-02.
• Results first posted 2021-03-10.
• 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

NCT02255474, titled “Bifocal Lenses In Nearsighted Kids,” is a completed randomized, triple-masked, parallel trial sponsored by Ohio State University. The registry lists enrollment as 294 and describes children ages 7 to 11 years old as the intended population. Biofinity soft spherical contact lenses were compared with Biofinity Multifocal D lenses with +1.50 D and +2.50 D adds.

The primary outcome was refractive error progression over 3 years, measured by cycloplegic autorefraction in both eyes. The registry reports a mixed models primary analysis and arm summaries from which unadjusted pairwise comparisons can be recalculated. Those estimates differ, so the sponsor’s analysis takes precedence. Secondary outcomes address peripheral defocus and axial length, among related measures. The registry record does not report key details including the full analysis plan, multiplicity handling, missing-data methods, or the original sample-size justification.