Evaluation of Adherence and Therapeutic Effectiveness of Bi-Flex Versus CPAP in Children With OSA: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Adherence and Therapeutic Effectiveness of Bi-Flex Versus CPAP in Children With OSA (NCT00458406), a randomized na study. The primary outcome is Minutes of Use Per Night at Month 1.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, single-center study of Bi-Flex versus CPAP in children with obstructive sleep apnea. Its design fields label masking as triple, while the study summary and arm descriptions use the term double-blind. Which people were masked, and how masking was maintained, are not reported in the registry record. The study is marked completed.

The registry reports enrollment of 60. For the primary outcome, results are posted for 43 participants in the Bi-Flex arm and 13 in the CPAP arm. The endpoint description also states that a study sample size of 45 in Bi-Flex and 15 in CPAP had 80% power to detect an effect size at least 0.85 using a 0.05 two-sided significance level. It further states that the 95% confidence interval for the difference between the means had a range of 1.282 standard deviations under that sample-size statement. These planning details are distinct from the observed group counts and results.

The study period is described as 3 months, and the primary endpoint was assessed at month 1. The registry lists additional measures including dropout, sleep-study results, comfort-related measures, and questionnaires. The detailed timing and measurement procedures for all outcomes are not reported in the registry record. The random sequence generation method, allocation concealment, analysis population, handling of missing observations, and any interim analyses are also not reported there.

Randomization can help balance prognostic factors across treatment groups, but it does not guarantee exact balance, particularly when group sizes differ. Masking may reduce biases related to treatment expectations or outcome assessment, but the registry does not identify the masked roles. Accordingly, the posted results describe the comparison that was recorded; they do not resolve uncertainties about implementation or analysis procedures that are absent from the record.

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: Sixty-nine consecutive families were approached for the study. Nine families declined the study. N=60 families were enrolled; N=4 of these were excluded due to various medical conditions. Of the remaining N=56, N=43 were enrolled into the Bi-Flex arm and N=13 were enrolled into the CPAP arm.

Month 1

Month 3

Analysis population for the primary outcome, as defined in the registry: The study sample size of 45 in the Bi-Flex group and 15 in the CPAP group had 80% power to detect an effect size ≥ 0.85 with a 0.05 two-sided significance level. In addition, with this sample size, the 95% CI for the difference between the 2 means had a range of 1.282 SD.

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 Minutes of Use Per Night at Month 1, measured over 1 month.

The primary endpoint was minutes of use per night at month 1. It measures device use as recorded in minutes, making it a direct adherence measure rather than a symptom score or sleep-study measure. The trial summary identifies adherence as the main reason for comparing Bi-Flex with CPAP: CPAP was described as the usual treatment, but as uncomfortable and often not tolerated. The study therefore asked whether the Bi-Flex approach was associated with greater use.

For Bi-Flex, the posted mean was 185.0 minutes per night, with a standard deviation of 165.0, among 43 participants. For CPAP, the mean was 201.0 minutes, with a standard deviation of 135.0, among 13 participants. The comparison is expressed as CPAP minus Bi-Flex, so the estimated difference of 16.0 minutes points toward a higher average in the CPAP group. The 95% confidence interval, from -72.42 to 104.4, indicates substantial uncertainty around that estimate.

As a general statistical point, an objective measure of device use can complement self-reported comfort or adherence because it records use rather than relying only on a participant’s account. The registry says objective compliance recordings were among the study measures, but the precise recording and data-processing procedures are not reported. A group mean also does not describe every participant’s use or the shape of the distribution. The large standard deviations relative to the means indicate considerable variation in recorded use within both groups.

7. Results Posted in the Registry

• CPAP: mean 201.00 versus 185.00 on control; difference 16.00 (95% CI -72.42 to 104.42), standardized effect d = 0.10; z-test p = 0.723.

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.

Drop Out Rate

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CPAP: 7.7% (1/13) versus 2.3% (1/43) on control; risk difference 5.4 percentage points (95% CI -9.8 to 20.5), risk ratio 3.31 (0.22–49.29); unadjusted two-proportion z-test p = 0.361.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CPAP and the control. The interval gives the range of effects that remain compatible with the data.

Change in ESS From Month 1 to Month 3

• 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:
  • CPAP: mean -2.30 versus -4.50 on control; difference 2.20 (95% CI -0.67 to 5.07), standardized effect d = 0.52; z-test p = 0.133.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CPAP and the control. The interval gives the range of effects that remain compatible with the data.

Change in NOSE Scale Score From Month 1 to Month 3

• 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:
  • CPAP: mean -5.70 versus -1.60 on control; difference -4.10 (95% CI -7.90 to -0.30), standardized effect d = -0.62; z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for CPAP than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the questions beyond device use, but their coverage in the record is incomplete. The listed outcomes include dropout, apnea hypopnea index, OSA 18 score, ESS, NOSE scale score, and Pediatric Quality of Life. Detailed group results are posted for dropout and changes in ESS and NOSE. Detailed results for the other listed measures are not reported in the registry record.

Across the posted secondary results, there is not a single uniform pattern that resolves the primary adherence comparison. The recalculated dropout and ESS comparisons have confidence intervals that include no difference. The NOSE comparison has a recalculated interval that does not include zero, while the registry’s reported Wilcoxon result is p > 0.05. That difference in presentation illustrates why the sponsor’s rank-based test and a mean-difference recalculation should not be treated as tests of precisely the same estimand. The secondary results do not establish that the primary adherence question has a different answer, and they do not substitute for unposted sleep-study results.

Secondary outcomes are commonly useful for describing other dimensions of a trial, but they generally carry less confirmatory weight when they are not designated as the primary endpoint or when many outcomes are examined. Testing multiple outcomes increases the chance that at least one apparently notable result arises by chance. The registry does not report a multiplicity adjustment or a hierarchy governing interpretation of secondary outcomes. The selected results should therefore be viewed as exploratory context rather than as a set of independent confirmations.

The registry’s summary identifies comfort and therapeutic efficacy as additional objectives, but the detailed results available in this record do not cover all of those objectives. In particular, a full account of secondary evidence cannot be inferred from the measures with posted numerical results alone.

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

• Drop Out Rate
• Change in Apnea Hypopnea Index (AHI; Number of Apneas and Hypopneas Per Hour of Sleep) From Month 1 to Month 3
• Obstructive Sleep Apnea (OSA) 18 Score
• Change in ESS From Month 1 to Month 3
• Change in NOSE Scale Score From Month 1 to Month 3
• Pediatric Quality of Life (PedQL)

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, the posted outcome is a mean and standard deviation for each group. A mean describes the average minutes of use per night, while the standard deviation describes how dispersed individual observations are around that average. The reported comparison is a mean difference, with CPAP minus Bi-Flex as its direction. A positive estimate therefore corresponds to a higher posted mean in CPAP; a negative estimate would correspond to a higher posted mean in Bi-Flex.

The unadjusted recalculation uses the displayed group summaries to estimate the difference and its uncertainty. It does not adjust for other participant characteristics or factors. The recalculated mean difference is 16.0 minutes, with a 95% confidence interval from -72.42 to 104.4 and p = 0.723. The registry’s own reported primary test is a two-sided t-test with p = 0.512. The registry does not supply the sponsor’s estimated difference or confidence interval. Since the posted summaries and the reported test result are not identical outputs, they should be recognized as separate presentations rather than assumed to be the same calculation.

A confidence interval gives a range of values compatible with the estimate under the analysis assumptions. In repeated use of the same method under its assumptions, a 95% confidence interval has a long-run coverage interpretation; it is not a statement that there is a 95% probability that the particular interval contains the true value. The interval includes zero, the value representing no mean difference, and extends into both negative and positive differences. Its breadth makes clear that the direction and size of any difference are uncertain.

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value above a conventional threshold is not evidence by itself that two treatments are equivalent. The registry does not report a prespecified equivalence margin or a non-inferiority framework.

For continuous outcomes, the recalculated planning illustrations use an observed effect as a reference and show hypothetical group sizes for selected fractions of that effect. These are planning calculations, not measurements of the trial’s performance. The assumptions stated for these illustrations are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The stated detectable effect is the chosen fraction of the observed effect. The original design’s full sample-size assumptions are not reported in the registry record, apart from the separate planning statement in the primary endpoint description.

For a binary outcome such as dropout, the comparison can be expressed as a risk difference: the proportion with the event in one group minus the proportion in the other. The posted recalculation for dropout estimates a risk difference of 0.054, with a 95% confidence interval from -0.098 to 0.205 and p = 0.361. The group counts are small, and estimates of proportions can be imprecise when events are few. The registry’s reported test for dropout is a chi-squared test with p > 0.05. The recalculated risk difference and the reported test are different descriptions of the comparison and should not be treated as interchangeable output.

The secondary continuous outcomes are listed with group means and standard deviations. Their reported sponsor analyses use Wilcoxon (Mann-Whitney) tests for ESS and NOSE change, whereas the simple recalculated comparisons use mean differences. A rank-based test evaluates differences in the distributions of ranks and does not test precisely the same quantity as a test of means under general conditions. Thus, differences in the numerical results or significance labels can reflect the analysis target and method as well as the data.

Why does variation matter?

Variation affects how precisely a group mean and a between-group difference can be estimated. When participant measurements vary widely, the mean can be uncertain even when the average is clearly calculable. For minutes of use, the standard deviations are 165.0 minutes for Bi-Flex and 135.0 minutes for CPAP. Those spreads are substantial relative to the observed group means, and the observed group counts are unequal. The resulting confidence interval is broad. A mean and standard deviation are useful summaries, but they do not show whether the observations are symmetric, clustered, or strongly influenced by unusually high or low values.

For counts or rates, over-dispersion is a general concern when variability exceeds what a simple model assumes. In general, a model that understates variation can make uncertainty appear too small. The registry does not report a count-based model for the primary endpoint, and the posted primary outcome is continuous minutes of use. No distributional diagnostic or robust analysis is described in the registry record, so there is no basis to say whether such alternatives were used.

What does randomization contribute?

Random allocation supports a causal comparison by reducing systematic differences between groups in expectation. It does not eliminate chance imbalances, missing data, nonadherence, or measurement limitations. The record identifies the study as randomized but does not report the sequence-generation or concealment methods, nor does it state whether results were analyzed by assigned group. Those omissions matter when assessing how closely the reported comparison follows the randomized design.

How should the planning illustrations be read?

Power calculations describe the chance that a specified statistical procedure will reject a null hypothesis under an assumed effect and other planning conditions. The posted planning illustrations ask how many participants per arm would be needed under stated assumptions for 80% or 90% power. They are not a retrospective measure of whether this trial had adequate power, and they are not observed power. As a general principle, planning for a smaller effect requires more participants, all else equal. The observed group summaries, confidence intervals, and prespecified clinical objectives remain more useful for interpreting the trial’s evidence than a retrospective power label.

11. Confidence Intervals and Precision

The primary comparison has a 95% confidence interval from -72.42 to 104.4 minutes for CPAP minus Bi-Flex. The point estimate is 16.0 minutes, but the interval extends well in both directions around that estimate. Values below zero would favor a higher average for Bi-Flex, while values above zero would favor a higher average for CPAP. Because the interval includes zero, the posted estimate does not establish a direction of difference.

The interval is also broad enough that the results do not pin down the magnitude closely. It includes differences that could be relevant in either direction, although the registry does not report a threshold for clinical importance. The observed variability and the unequal group counts are important context for this imprecision: the standard deviations were 165.0 minutes and 135.0 minutes, and the primary results include 43 Bi-Flex participants and 13 CPAP participants.

Confidence intervals are not a guarantee that the true effect lies within the displayed endpoints. They quantify uncertainty under the analysis method and its assumptions. The registry does not report adjustment for covariates, sensitivity analyses, or details of missing-data handling that would show how robust the interval is to alternative choices. The sponsor’s own primary analysis reports p = 0.512 but does not include an effect estimate or confidence interval in the posted result. The recalculated interval should therefore be understood as an unadjusted summary-based estimate, not as a replacement for an unreported sponsor interval.

Precision and statistical significance are related but not identical. An estimate can be imprecise even when its point estimate appears small, and a narrow interval would still need to be judged against a clinically meaningful threshold. Here, the interval’s inclusion of both negative and positive values reinforces that the estimated comparison is uncertain rather than demonstrating equality.

12. Planning a Similar Trial: Sample Size

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

The planning figures for these comparisons are stated as participants per arm, not total events. The general assumptions listed for the planning illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to a stated fraction of the observed effect. The original trial design assumptions are not reported in the registry record, apart from the separate sample-size statement in the primary endpoint description.

The 80% power column means the illustrative number of participants per arm under which the assumed test would have an 80% chance of detecting the chosen effect, if the planning assumptions and effect were correct. The 90% column gives the corresponding target for a 90% chance. These are prospective design concepts expressed as hypothetical sample-size requirements; they do not show that an observed result had a particular probability of being correct or of being detected.

Each effect fraction changes the planning question. Planning for 75% of the observed effect asks about a smaller effect than planning for 100%; planning for 50% asks about a still smaller one. Smaller effects generally require more participants to distinguish them from random variation at the same significance level and power target. For example, the primary-outcome illustration lists 1,547 participants per arm for planning around 100% of the observed effect at 80% power, and 6,188 participants per arm for 50% of that effect at 80% power.

These figures are planning illustrations based on the observed estimate, not the trial’s original recruitment target. They are not observed power. The endpoint description separately states a sample-size plan of 45 in Bi-Flex and 15 in CPAP, with 80% power to detect an effect size at least 0.85 at a 0.05 two-sided significance level. The registry does not provide enough detail to reconcile that statement with every assumption used in the recalculated illustrations.

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 = 16.000; pooled standard deviation σ = 158.824.
2. n = 2 × (1.96 + 0.842)² × 158.824² / 16.000² = 1,546.8, rounded up to 1,547 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 <- 16                      # observed difference in means
sigma <- 158.823801742686                     # 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(458406)
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 = 1,547 (80% power), 2,071 (90% power)
 75% of observed effect: n per arm = 2,750 (80% power), 3,682 (90% power)
 50% of observed effect: n per arm = 6,188 (80% power), 8,283 (90% power)
power.t.test: 1547.7 
Simulated power at n = 1,547 per arm: 0.805 (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

For the primary outcome, the registry reports the sponsor’s analysis as a two-sided t-test with p = 0.512. The summary-based recalculation gives a mean difference of 16.0 minutes for CPAP minus Bi-Flex, a 95% confidence interval from -72.42 to 104.4, and p = 0.723. Both reported p-values are above 0.05, but they are not identical.

The recalculation uses the posted group means, standard deviations, and group counts as an unadjusted comparison. The registry does not report the sponsor’s estimated difference, confidence interval, or further analytic details for this endpoint. It is therefore not possible to determine from the record why the reported p-values differ or whether the sponsor used additional information or a different procedure. The difference in p-values should not be interpreted as evidence of a different clinical conclusion by itself.

The sponsor’s analysis is the registry’s reported inferential result. The recalculation adds an estimate and interval derived from the posted summaries, but it cannot reproduce details that are not recorded. The registry does not report adjusted analyses or sensitivity analyses for the primary endpoint. Reading the reported test together with the recalculated estimate and its broad interval keeps the emphasis on both the trial’s own reported analysis and the uncertainty visible in the group summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several outcome measures, including the primary adherence endpoint and secondary measures covering dropout, sleep-study indices, symptoms, and quality of life. It does not report whether the analysis plan used a hierarchy, a family-wise error adjustment, or another approach to multiplicity. Without such information, a nominal p-value from an individual secondary analysis should not be read as if it were the only statistical question posed by the study.

Multiplicity matters because examining many outcomes can increase the chance of at least one result appearing noteworthy by chance, even when no corresponding effect exists. This is a general statistical concern, not a claim that any particular posted finding is false. The registry does not report how many hypotheses were prespecified, whether analyses were exploratory, or whether outcome selection changed after data review. The analysis plan and any protocol amendments are not reported in the registry record.

Missing-data handling is also not reported. The group counts for the primary endpoint are 43 in Bi-Flex and 13 in CPAP, while the registry reports enrollment of 60. The record does not explain the relationship between enrollment and the outcome counts, identify why observations may be absent, or state whether all randomized participants were analyzed. It does not describe imputation, complete-case analysis, or sensitivity analyses for missing outcomes. No participant-flow explanation is available in the registry record, so the effect of missingness on the estimates cannot be assessed from these results alone.

The analysis population is not reported. The record does not state whether the primary analysis followed randomized assignment, included participants who used the assigned device, or used another definition. This distinction can matter in randomized trials because excluding participants after randomization may undermine the balance that randomization is intended to create. The randomization procedure and allocation concealment are also not reported, leaving additional design details unresolved.

Interim analyses and stopping rules are not reported in the registry record. That absence does not establish that interim analyses occurred or that they did not occur; it means the available record does not describe them. Overall, the missing analysis details limit the ability to judge prespecification, robustness, and the possible influence of missing observations or multiple testing.

16. 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 0% reporting threshold.

The registry records zero serious adverse events among 43 participants in the Bi-Flex group and zero among 13 participants in the CPAP group. It also records zero other adverse events in each group. These are the adverse-event counts posted for the groups, not proof that no adverse experiences occurred outside the registry’s reporting definitions or collection process.

Zero recorded events do not establish that the risk is zero. When an event is uncommon, a study with limited group counts may observe no cases even when some underlying risk exists. The record does not provide event-specific terms, a detailed safety assessment method, or information about how adverse events were solicited and followed. Death counts are not reported in the registry record.

These figures should be read as a description of the adverse events recorded in this trial, with the available follow-up and reporting details. They do not support a broad comparative safety conclusion, especially because the record does not describe adverse-event definitions, exposure time, or a formal analysis of between-group safety differences.

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

The posted primary result estimates average device use at month 1 in the randomized Bi-Flex and CPAP groups. The observed means were 185.0 and 201.0 minutes per night, respectively, and the recalculated difference was 16.0 minutes for CPAP minus Bi-Flex. The 95% confidence interval, from -72.42 to 104.4, is broad and includes no difference. These data therefore provide an uncertain estimate of the direction and size of any average adherence difference.

This result does not establish that Bi-Flex improves adherence relative to CPAP. The point estimate is in the opposite direction, but the interval is too broad to support a precise ranking. It also does not demonstrate that the treatments are equivalent or that their adherence effects are clinically indistinguishable. Equivalence would require a prespecified margin and an analysis designed for that question; neither is reported in the registry record.

The endpoint concerns recorded minutes of use, not every aspect of treatment experience or therapeutic efficacy. The study summary identifies sleep-study findings, comfort, and questionnaires as additional interests. Selected secondary results are available, but detailed results for all listed outcomes are not reported in the registry record. The primary adherence estimate cannot answer whether sleep-study outcomes were similar or whether participants found one approach more comfortable.

Nor does the result establish what would happen in other settings or populations. The registry describes a single-center study in children with OSA, and the results are based on the group counts posted for the primary endpoint. Generalizability depends on details such as eligibility, treatment delivery, and patient characteristics that are not fully described in the record.

The appropriate reading is bounded: the trial recorded the stated group means and an imprecise between-group estimate, while the registry’s own test reports p = 0.512. The summaries do not provide a precise estimate of an adherence advantage in either direction. Interpretation of efficacy, comfort, safety, and broader clinical relevance requires evidence beyond this primary endpoint and the details available in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates the difference between estimating an effect and deciding whether a statistical test crosses a threshold. The primary estimate is 16.0 minutes, but its 95% confidence interval extends from -72.42 to 104.4. The interval communicates that the data are compatible with a range of differences, not merely a single point estimate. It also shows why a result that does not meet a conventional significance threshold should not be translated into proof of no difference.

The group summaries also make the role of variability visible. Standard deviations of 165.0 and 135.0 minutes indicate considerable spread in use, while the primary outcome groups are unequal in size. Both features affect the precision of a comparison. Reporting the estimate and interval alongside the group means gives a more informative statistical account than a p-value alone.

The record provides an opportunity to distinguish sponsor-reported analyses from summary-based recalculations. The reported primary p-value is 0.512; the recalculated p-value is 0.723. A transparent account notes both, explains what the recalculation uses, and avoids implying that the registry contains enough detail to reproduce every aspect of the sponsor’s analysis.

Finally, the trial raises broader issues common to clinical research: how adherence should be measured, how multiple outcomes are interpreted, and how missing observations and analysis populations affect confidence in results. The registry identifies these questions but does not report all the information needed to resolve them. That distinction between what results show and what remains undocumented is central to careful statistical 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 primary outcome results are based on unequal group counts: 43 for Bi-Flex and 13 for CPAP. The registry reports enrollment of 60 but does not explain how that figure relates to the counts used for the primary endpoint. Without a participant-flow account, the reasons for the difference and the possible consequences for interpretation are unclear.

The primary endpoint has substantial observed variation and a broad confidence interval. The registry does not report a clinically important difference in minutes of use, so the practical importance of the range of compatible estimates cannot be determined from the record alone. The primary endpoint is measured at month 1, while the study is described as lasting 3 months; the registry does not provide a detailed account of adherence over the full study period in the posted primary result.

Important design and analysis details are absent. The record does not describe the randomization sequence, concealment, which roles were masked, the analysis population, missing-data methods, or sensitivity analyses. It labels masking as triple while the narrative uses double-blind, without identifying the masked roles. These gaps restrict assessment of potential bias and robustness.

The results available for secondary outcomes are incomplete, and no multiplicity procedure is reported. Some listed outcomes, including apnea hypopnea index and Pediatric Quality of Life, do not have detailed results in this record. The registry’s reported primary test also lacks an accompanying sponsor effect estimate and interval, making direct comparison with the summary-based recalculation limited. The single-center setting further narrows the context in which these results can be interpreted, while eligibility and treatment-delivery details are not fully reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of Adherence and Therapeutic Effectiveness of Bi-Flex Versus CPAP in Children With OSA — NCT00458406.
• Registry record last updated 2019-10-02; status last verified 2019-09.
• Results first posted 2014-04-01.
• 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

The registry describes a completed randomized, parallel-group study comparing Bi-Flex with CPAP in children with obstructive sleep apnea. The study summary identifies adherence as the primary objective and minutes of use per night at month 1 as the primary endpoint. Enrollment is listed as 60, and the primary outcome results are posted for 43 Bi-Flex participants and 13 CPAP participants.

The observed mean use was 185.0 minutes per night with Bi-Flex and 201.0 minutes with CPAP. The recalculated mean difference, CPAP minus Bi-Flex, was 16.0 minutes, with a 95% confidence interval from -72.42 to 104.4 and p = 0.723. The registry’s reported two-sided t-test gives p = 0.512. The interval is broad and includes no difference, so the primary comparison is imprecise.

Selected secondary results are posted, but several listed outcomes and key analysis details are not reported in the registry record. The available data describe the recorded comparison; they do not establish equivalence, answer every therapeutic question, or resolve the limitations associated with missing design and analysis information.