Transcend Auto vs Commercially Available Device Clinical Evaluation for Treatment of Obstructive Sleep Apnea (OSA): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Transcend Auto vs Commercially Available Device Clinical Evaluation for Treatment of Obstructive Sleep Apnea (OSA) (NCT01799265), a randomized na study. The primary outcome is Mean Apnea Hypopnea Index (AHI) During Treatment.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, single-masked crossover study of Transcend Auto and Respironics REMstar Auto with C-Flex. A crossover design means that participants receive both treatments in different periods or sequences, so each participant can contribute observations under each device. The two listed sequences were Transcend followed by REMstar and REMstar followed by Transcend. The primary outcome timeframe was the first and second night sleep study.

In this design, treatment sequence matters to interpretation. A comparison may use the within-participant relationship between the two measurements, while the order of treatment may also be relevant. The registry record does not report the analysis model used to account for pairing, sequence, period, or possible carryover effects. It also does not describe the masking procedure beyond identifying the study as single-masked.

The recorded enrollment was 41. The posted primary outcome summaries report 35 observations for Transcend and 35 for REMStar. Those counts do not, by themselves, establish how many participants contributed paired observations or how missing measurements were handled. The analyzed population and the reasons for any difference between enrollment and outcome counts are not reported in the registry record.

The study is marked completed, with a start date of 2013-02-27 and primary completion date of 2013-06-10. Its stated purpose was to determine whether Transcend Auto was as effective in treating obstructive sleep apnea as another marketed device. The registry record does not report a sample-size justification for the original trial or the planned details of its statistical analysis beyond the posted non-inferiority test description.

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 Mean Apnea Hypopnea Index (AHI) During Treatment, measured over first and second night sleep study.

The primary outcome is mean apnea hypopnea index, or AHI, during treatment. AHI is defined in the registry record as the number of apneas plus the number of hypopneas divided by total sleep time in hours. It is a continuous measure, with a minimum score of zero; higher values indicate more apnea and hypopnea events per hour of sleep. The record gives AHI >= 15 as an example threshold used to define obstructive sleep apnea.

AHI is used to quantify breathing events during each sleep study under each device. Comparing treatment-period means gives a summary of the average measured event rate, while the spread of participant measurements indicates how much individual results vary. The registry record says AHI was measured by the devices and independently by a central laboratory. It does not make clear which measurement source underlies the posted arm summaries.

Because this is a crossover evaluation, the same participant may be measured under both devices. That offers a way to compare treatments while accounting for stable differences between participants, if the analysis uses the paired data appropriately. The posted summary means alone do not show whether that pairing was incorporated. Nor does a similar average AHI by itself establish non-inferiority: that interpretation depends on the prespecified margin and the sponsor’s analysis, whose numerical estimate and confidence interval are not reported in the registry record.

7. Results Posted in the Registry

• REMStar: mean 2.00 versus 2.10 on control; difference -0.10 (95% CI -1.13 to 0.93), standardized effect d = -0.05; z-test p = 0.850.

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.

Mean Differences Between Polysomnography (PSG) and Device Measures of Apnea Index (AI) and Hypopnea Index (HI)

• 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:
  • REMStar: mean 0.20 versus -0.70 on control; difference 0.90 (95% CI -0.03 to 1.83), standardized effect d = 0.45; z-test p = 0.057.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between REMStar and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the focus beyond mean treatment AHI. They cover unanticipated adverse device effects and differences between polysomnography and device measures of apnea and hypopnea indices. The posted continuous measurement-difference outcome gives a comparison of the two device summaries, while the adverse-effect information is reported separately. Together, these outcomes provide additional descriptive context, but they address distinct questions from the primary comparison of treatment AHI.

The secondary measurement result should not be treated as a repeat test of the primary endpoint. A measurement difference between PSG and a device is about how the methods compare, not directly about whether one treatment produces a lower or higher mean AHI than the other. Similarly, adverse device effects concern safety reporting rather than the primary efficacy measure. The secondary results therefore neither confirm nor overturn the primary result; they add dimensions that would need their own prespecified interpretations.

Unadjusted secondary results carry less weight as confirmatory evidence when several outcomes are examined. General statistical principle: considering multiple outcomes creates more opportunities for chance findings, and interpretation is stronger when multiplicity handling and the intended hierarchy of outcomes are prespecified and reported. The registry record does not report a multiplicity adjustment or a hierarchy that would clarify how secondary findings were intended to support conclusions.

The record lists three outcome measures, including the primary outcome, and identifies two secondary outcome categories. It does not report detailed sponsor analyses for the posted continuous secondary comparison. Its recalculated estimate and interval are therefore descriptive and unadjusted. The number and nature of secondary measures can help readers understand the breadth of assessment, but incomplete analysis details mean that no single secondary result should be promoted to a definitive conclusion about the devices or the primary question.

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

• Unanticipated Adverse Device Effects
• Mean Differences Between Polysomnography (PSG) and Device Measures of Apnea Index (AI) and Hypopnea Index (HI)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference describe?

A mean difference subtracts one group’s average from the other’s, with the direction determined by which treatment is set as the reference. The posted primary means are 2.1 for Transcend and 2.0 for REMStar. The recalculated difference is reported as -0.1 for REMStar relative to Transcend. A value close to zero indicates that the two posted averages are close, but the mean difference does not show whether individual paired responses consistently favor one device or vary in both directions. It also does not show whether a clinically acceptable non-inferiority margin has been met.

Why does the crossover design matter?

In a crossover study, a participant receives both treatments, and the comparison can use each participant as their own reference. General statistical principle: accounting for this pairing can reduce the influence of stable differences between participants and can change the uncertainty of the treatment contrast. The size and direction of that change depend on the correlation between measurements from the same participant. The registry record gives arm-level means and standard deviations, but not paired differences, their standard deviation, or the covariance between measurements. The simple recalculation therefore cannot reproduce a paired analysis.

Order and period may also matter in a crossover study. For example, the measurement during one night could be affected by the order in which devices were used or by a period effect. This is a general design consideration, not a finding about this trial. The record identifies both treatment sequences but does not report whether the sponsor assessed sequence, period, or carryover effects.

What does the confidence interval contribute?

A confidence interval expresses uncertainty around an estimated effect. General explanation: under the assumptions of the method, intervals constructed in this way would cover the underlying parameter at the stated rate over repeated studies. For the primary summary-based recalculation, the interval runs from -1.135 to 0.935. Its width reflects uncertainty in the estimated difference; values on both sides of zero are compatible with the calculation. The interval is not the sponsor’s reported non-inferiority interval, which is not reported in the registry record.

The reported unadjusted p-value of 0.85 tests a zero-difference null in the recalculation. A large p-value is not proof that treatments are identical. It means that the observed summaries are not unusual under that null, given the calculation’s assumptions. The result should not be translated into a probability that the null is true or a probability that the devices are equivalent.

How does non-inferiority differ from a test of no difference?

A non-inferiority test evaluates whether an intervention’s performance is not worse than a comparator beyond a prespecified margin. The margin defines the largest difference that would still be accepted for the purpose of that test. General statistical principle: the test conclusion depends on the direction of the contrast, the margin, and the uncertainty around the estimate, not merely on whether a conventional test of zero difference is statistically significant. The registry record reports a sponsor one-sided t-test for non-inferiority with p = .05, but the margin and the sponsor’s estimate and confidence interval are not reported. The recalculated two-group comparison does not replace that analysis.

Why can over-dispersion matter?

General explanation: when outcome variability is greater than a statistical model assumes, standard errors can be too small and confidence intervals too narrow if the extra variability is ignored. AHI is a count-derived rate, but the registry record reports a mean and standard deviation and the recalculation treats the outcome as continuous. There is no posted assessment of distributional shape, model fit, or over-dispersion, so no conclusion about those features can be drawn. This general consideration is not evidence that over-dispersion affected the trial’s results.

What can the planning calculations tell a reader?

The planning figures illustrate how many participants per arm would be required under stated assumptions to detect specified fractions of the observed effect. They are not a reconstruction of the original trial design. The original sample-size justification is not reported in the registry record. These calculations depend on assumptions such as equal allocation, a two-sided significance level of 0.05, and a normal approximation. They also assume that the selected fraction of the observed effect is the target difference. Such calculations describe planning scenarios, not evidence that an effect exists or that a completed study had a particular probability of detecting it.

11. Confidence Intervals and Precision

The recalculated primary mean difference is -0.1, and its 95% confidence interval extends from -1.135 to 0.935. The interval includes zero and spans values on both sides of no difference. Thus the point estimate alone gives an incomplete account: it is close to zero, but the uncertainty permits a range of possible differences under the recalculation’s assumptions.

Precision concerns the range of values compatible with the data and method, not whether a result is important or acceptable. The posted standard deviations, 2.0 for Transcend and 2.4 for REMStar, describe variability within the reported device summaries. They do not provide the variability of paired within-participant differences, which would be especially relevant for this crossover design. Because the paired covariance is not reported, the recalculated interval may not reflect the uncertainty from the sponsor’s intended crossover analysis.

The interval also cannot establish non-inferiority without the sponsor’s margin and the corresponding analysis. A confidence interval used for non-inferiority must be interpreted against that margin and in the appropriate direction. The registry record does not report the margin or the sponsor’s confidence interval. The reported one-sided test p-value of .05 is not enough on its own to assess the precision of the sponsor’s estimated treatment contrast.

For the secondary measurement-difference outcome, the recalculated estimate is 0.9, with a 95% confidence interval from -0.028 to 1.828. This interval also includes zero. It is an unadjusted comparison based on posted summaries, not a confirmatory conclusion about agreement. In both cases, confidence intervals quantify statistical uncertainty under the calculation used; they do not account for missing or unreported design information.

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 table and curve translate an assumed target effect into a planning illustration. The figures are participants per arm, not total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a specified fraction of the observed effect as the effect to detect. The registry record does not report the original trial’s sample-size assumptions or justification, so these planning figures should not be read as its design target.

The 80% power column gives the number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the selected effect under the stated assumptions. The 90% power column uses a higher target chance of detection and therefore gives a larger planning requirement for the same effect. For the primary outcome, the row for 100% of the observed effect gives 7,661 participants per arm for 80% power and 10,256 participants per arm for 90% power. For 75% of the observed effect, the corresponding figures are 13,619 and 18,232. For 50% of the observed effect, they are 30,643 and 41,021.

Smaller target effects require more participants because they are harder to distinguish from ordinary sampling variation. The curve visualizes that relationship across the selected effect assumptions. These calculations are planning illustrations based on the observed effect, not observed power. They do not describe the chance that the completed trial found a true effect, nor do they validate the original study’s size. The observed enrollment was 41, which is separate from these hypothetical planning requirements and should not be compared with them as though the assumptions were the study’s original protocol.

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 = -0.100; pooled standard deviation σ = 2.209.
2. n = 2 × (1.96 + 0.842)² × 2.209² / -0.100² = 7,660.5, rounded up to 7,661 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 <- -0.1                      # observed difference in means
sigma <- 2.20907220343745                     # 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(1799265)
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 = 7,661 (80% power), 10,256 (90% power)
 75% of observed effect: n per arm = 13,619 (80% power), 18,232 (90% power)
 50% of observed effect: n per arm = 30,643 (80% power), 41,021 (90% power)
power.t.test: 7661.5 
Simulated power at n = 7,661 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. Analyses Reported by the Sponsor

The sponsor’s posted analysis is identified as a one-sided t-test for non-inferiority, with p = .05. The registry record does not provide a numerical sponsor estimate, confidence interval, test statistic, or non-inferiority margin. As a result, the specific comparison between the sponsor’s conclusion and a stated acceptable difference cannot be reconstructed from the posted analysis details.

The recalculated primary comparison uses the posted group means and standard deviations. It gives a mean difference of -0.1, a 95% confidence interval from -1.135 to 0.935, and an unadjusted p-value of 0.85. This is a simple unadjusted recalculation from summary statistics. It does not incorporate the paired participant-level structure that may be important in a crossover design, and it is not the sponsor’s non-inferiority test.

The sponsor’s own analysis takes precedence where the recalculation differs, as it does in this record. That does not make the sponsor result independently verifiable: the missing margin and numerical result prevent a full assessment. The recalculation is useful as a separate description of the posted averages and their uncertainty under its assumptions, not as a replacement for the analysis reported by the sponsor.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists the primary mean AHI outcome and two secondary outcome categories. It does not report a multiplicity strategy, such as an adjustment to account for testing multiple outcomes, or a hierarchy governing the interpretation of secondary measures. Without such information, the chance of at least one apparently notable result across several analyses is difficult to assess. This is a general concern with multiple testing, not a claim that a particular posted finding is false.

The record reports one sponsor analysis, identified as a one-sided t-test for non-inferiority. It does not give the full statistical analysis plan, the non-inferiority margin, or enough numerical detail to reproduce that test. The trial’s original sample-size justification and assumptions are also not reported in the registry record. The planning calculations based on the observed effect are separate illustrations and do not fill in those missing protocol details.

Missing-data handling is not reported in the registry record. Although the trial enrolled 41 and the primary outcome summaries list 35 observations for each device, the record does not explain the count difference, state whether all included participants contributed both device measurements, or describe any imputation or exclusion rules. It also does not identify the analysis population used for the primary result. In a crossover study, knowing whether observations are paired and how incomplete pairs are handled can materially affect both the estimate and its precision.

The record does not report whether the sponsor assessed sequence, period, or carryover effects, or how the single masking designation was implemented. Nor does it state whether the primary endpoint was analyzed using a paired model or another approach. These omissions limit reproducibility and make it difficult to judge whether the posted summaries represent the intended analysis. They do not show that the analyses were inappropriate; they mark information that is not reported in the registry record.

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.

Most frequent non-serious adverse event terms

The posted serious adverse event figures list zero serious events among 20 participants at risk for Transcend and zero among 21 at risk for REMStar. These are the registry’s reported counts for the safety groups. The safety denominators differ from the 35 observations listed for each device in the primary outcome summaries, so the figures should not be treated as if they came from the same analysis population without further information.

For other adverse events, the record lists one affected participant among 20 at risk for Transcend and none among 21 at risk for REMStar. Deaths are not reported in the registry record. The record does not provide further detail about the non-serious event or a list of serious event terms.

Zero reported serious events in these groups is a description of the recorded counts, not proof that serious harms cannot occur or that the devices have identical safety profiles. The safety information is limited by the short sleep-study timeframe, the reported counts, and the absence of additional event detail in the registry record. It should be read as an account of what was posted for this trial, not as a general safety estimate.

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

The posted primary summaries show similar mean AHI values during the two device treatment periods: 2.1 for Transcend and 2.0 for REMStar. The unadjusted recalculation estimates a mean difference of -0.1, with a confidence interval that includes zero. These results describe the observed summaries and their uncertainty under the recalculation method. They do not establish that the devices are identical.

The trial was framed as a non-inferiority evaluation, but non-inferiority cannot be inferred simply because the means are close or because a conventional test does not show a difference. It requires comparison with a prespecified margin using an appropriate analysis. The sponsor’s reported one-sided test has a p-value of .05, yet the margin and numerical estimate are not reported in the registry record. The sponsor’s non-inferiority conclusion therefore cannot be fully assessed from the available details.

The crossover structure is important because each participant may have received both devices. Without paired results and details about the analysis of sequence and period, the summary-based recalculation may not capture the design’s intended comparison. The recorded enrollment and posted outcome counts also do not explain how many participants contributed complete paired measurements.

These results concern treatment-period sleep-study measurements. They do not establish long-term outcomes, effects on symptoms or daily functioning, or results in populations not described in the registry record. The record’s secondary measurement and adverse-event results address additional questions but do not expand the primary endpoint into a broader clinical outcome. No treatment recommendation follows from these posted statistics. The appropriate statistical reading is limited to the recorded short-term measurements, the sponsor’s incomplete non-inferiority reporting, and the uncertainty created by unavailable design and analysis details.

18. Why This Trial Matters Statistically

This trial is statistically notable because its crossover design can support within-participant comparisons, while the posted primary results are presented as arm-level means and standard deviations. The distinction matters: a paired comparison depends on how measurements from the same participant relate to one another, and that relationship is not recoverable from separate means and standard deviations alone. Readers therefore need to distinguish the registry’s sponsor analysis from a simple recalculation of the posted summaries.

The non-inferiority framing also highlights why a result that appears close to zero is not enough. A non-inferiority conclusion depends on an explicit margin and a corresponding estimate with uncertainty. The registry record identifies the sponsor’s one-sided test but does not report those key details. This makes transparent reporting particularly important: the label of a method cannot substitute for the margin and result needed to interpret it.

The planning illustrations make a related statistical point. Sample-size requirements depend strongly on the target effect, with smaller effects requiring more participants under the stated assumptions. Since those calculations use the observed effect and are not the original design justification, they illustrate a planning relationship rather than explain why the study enrolled its recorded number of participants.

Finally, the difference between the primary outcome counts and safety denominators, together with unreported missing-data and analysis-population details, limits reconstruction of the analytic sample. These features make the trial a useful example of how design, reporting, and uncertainty all shape interpretation. The posted results can be described precisely, but stronger conclusions require details the registry record does not report.

19. Limitations

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

Several limitations are specific to interpreting this trial’s record. The crossover sequence is described, but the paired participant-level results are not posted. The summary-based recalculation cannot use the covariance between device measurements, and the registry record does not describe how the sponsor modeled the crossover structure. It is therefore not possible to verify from the posted summaries whether sequence, period, or carryover effects were considered.

The registry record does not state which AHI source contributes to the posted primary means, even though it says AHI was measured by the devices and independently by a central laboratory. The primary outcome description also does not provide an analyzed population or details about missing measurements. The enrollment of 41 and primary outcome counts of 35 for each device cannot be reconciled from the record alone.

The non-inferiority margin and sponsor’s numerical estimate and confidence interval are not reported, limiting assessment of the study’s stated inferential objective. The original sample-size justification is also absent. Planning figures based on the observed effect do not establish what assumptions informed the trial’s enrollment.

Additional limitations include the short timeframe of the primary measurement, the lack of reported multiplicity handling for secondary outcomes, and limited detail on adverse events. The registry record marks the study single-masked but does not explain how masking was carried out. These are limitations of the available reporting; they do not establish that the underlying trial failed to address these matters.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Transcend Auto vs Commercially Available Device Clinical Evaluation for Treatment of Obstructive Sleep Apnea (OSA) — NCT01799265.
• Registry record last updated 2025-01-13; status last verified 2022-10.
• Results first posted 2025-01-13.
• 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

NCT01799265 is a completed randomized, single-masked crossover study comparing Somnetics Transcend Auto with Respironics REMstar Auto with C-Flex for obstructive sleep apnea. It enrolled 41 participants and used two treatment sequences across the first and second night sleep studies.

The primary outcome was mean AHI during treatment. Posted means were 2.1 for Transcend and 2.0 for REMStar, with 35 observations reported for each device. A summary-based, unadjusted recalculation gives a mean difference of -0.1 and a 95% confidence interval from -1.135 to 0.935. The sponsor’s own analysis is reported as a one-sided non-inferiority t-test with p = .05, but its margin and numerical effect estimate are not reported.

The record also includes secondary measurement and adverse-event outcomes. Interpretation is constrained by unavailable paired results, missing-data and analysis-population details, and the absence of a reported multiplicity plan.