Modified Adaptive Servoventilation (ASV) Compared to Conventional ASV: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Modified Adaptive Servoventilation (ASV) Compared to Conventional ASV (NCT01405313), a randomized na study. The primary outcome is Apnea/Hypopnea Index (AHI).

2. Clinical Question

The trial is listed as randomized, unmasked, and crossover. In a crossover design, participants receive more than one study condition, so observations may be related within the same participant. The posted group summaries do not show the paired participant-level values or explain how that relationship was handled in the analyses. The registry lists oxygen desaturation index (ODI) as a secondary outcome. These endpoints describe physiological signals over a night; they do not, by themselves, establish effects on symptoms, daily functioning, or longer-term health outcomes.

3. Trial Design

The registry describes a randomized, unmasked crossover study of modified and conventional ASV. Enrollment is listed as 21. The study status is completed, and the listed start and primary-completion dates are 2011-07 and 2011-09. The phase is recorded as NA. ResMed is listed as the sponsor. These are registry entries and do not establish the trial’s conduct beyond what the record states.

The intervention arms are devices. Modified ASV is described as an enhanced ASV algorithm that includes auto-adjusting expiratory pressure. Conventional ASV is described as the current predicate ASV algorithm. The primary endpoint is AHI over one night, and the secondary endpoint is ODI over one night. Both are reported as means with standard deviations and use events per hour as the unit.

Randomization can reduce systematic differences in the assignment of study conditions, while crossover designs can allow within-participant comparisons. As a general statistical point, crossover analyses need to account for the dependence between measurements from the same participant. The registry record does not report the order or sequence of treatment periods, any washout, the handling of period or sequence effects, or whether the posted summaries reflect paired observations. It also does not report details of allocation concealment or any masking; the study is explicitly listed as having no masking.

The record lists a sponsor analysis using a one-sided t-test on the mean difference in final values, characterized as a non-inferiority or equivalence analysis. It does not report the prespecified margin or enough detail to determine the exact hypothesis being tested. The registry record does not report the original sample-size justification, the trial’s detailed statistical analysis plan, or whether interim analyses were conducted. The posted summaries therefore support a description of the recorded results, but not a full reconstruction of the planned analysis.

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: All enrolled participants continued through to group assignment.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All 21 patients completed the cross over study design

6. Primary Endpoint

The registry lists the primary outcome as Apnea/Hypopnea Index (AHI), measured over One night.

The primary endpoint is the apnea/hypopnea index (AHI), reported as events per hour of sleep over one night. The registry describes calculating it from physiological sleep signals, including pulse oximetry, respiratory effort, and nasal flow. Apneas are counted when respiratory flow is reduced by >90% for at least 10 seconds. Hypopneas are counted when respiratory flow is reduced by >30% for at least 10 seconds with a 4% oxygen saturation reduction. The total counted events are divided by hours of sleep.

AHI is used as a physiological measure of breathing events during sleep. Expressing the count per hour of sleep accounts for differing amounts of recorded sleep time in the definition of the endpoint. It is a rate measure, not a direct count of events over an identical duration for every participant. The registry reports group means and standard deviations, but does not provide participant-level measurements or the distribution of individual values.

The modified ASV group’s posted mean AHI is 3.9 events per hour, with a standard deviation of 4.7; the conventional ASV group’s mean is 6.4, with a standard deviation of 10.9. These descriptive summaries do not alone establish how the crossover comparison was analyzed, how precise the within-participant difference is, or whether a prespecified non-inferiority or equivalence criterion was met. The registry record does not report a clinical threshold for interpreting the size of an AHI difference.

7. Results Posted in the Registry

• Conventional ASV AHI: 6.40 versus 3.90 (Events per hour) on control; rate ratio 1.64 (95% CI 1.25–2.16, approximate, Poisson model); 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.

Oxygen Desaturation Index (ODI)

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Conventional ASV ODI: 8.20 versus 5.20 (Events per hour) on control; rate ratio 1.58 (95% CI 1.24–2.00, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for Conventional ASV ODI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists ODI as a secondary endpoint, measured as events per hour over one night. Its posted group summaries and sponsor analysis follow a pattern in which the modified ASV group has a lower mean rate than the conventional ASV group, consistent in direction with the primary AHI summaries. The secondary analysis is reported as a one-sided t-test on mean difference in final values, labeled as non-inferiority or equivalence. Its margin and confidence limits are not reported.

This directional consistency can be considered alongside the primary endpoint, but it does not independently establish the primary result or resolve the limitations of its analysis. ODI measures oxygen desaturation events, while AHI counts apneas and hypopneas using the registry’s stated criteria. The measures are related to physiological breathing during sleep, but they are not interchangeable endpoints. Their agreement in direction is not a substitute for a clearly specified primary hypothesis and appropriate analysis.

The registry lists one secondary outcome and reports an unadjusted p-value for it. Unadjusted secondary results carry less weight because testing multiple outcomes or analyses can increase the chance of finding a nominally noteworthy result by chance. In general, multiplicity procedures or a prespecified hierarchy can help control that issue, but the registry record does not report whether such a plan existed or was used. The secondary endpoint should therefore be interpreted as supportive descriptive context, rather than as an independent confirmation of efficacy or equivalence.

The same concerns that affect the primary analysis also matter: the crossover dependence, analysis population, missing-data handling, and non-inferiority or equivalence margin are not detailed in the record. The secondary result cannot fill those reporting gaps. No clinical conclusion should be drawn from the endpoint pattern alone.

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

• Oxygen Desaturation Index (ODI)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents group means and standard deviations for the primary and secondary endpoints, and reports a sponsor analysis for each. It also permits an unadjusted rate-based recalculation. Those approaches answer different statistical questions and rely on different assumptions. The crossover design makes the distinction especially important because measurements from the same participant may be related.

What does a mean and standard deviation describe?

A mean describes the average of the measured endpoint within a group. The standard deviation describes how spread out individual measurements are around that mean. For primary AHI, the posted means are 3.9 for modified ASV and 6.4 for conventional ASV; the respective standard deviations are 4.7 and 10.9. These summaries describe the observed groups but do not supply the distribution of paired changes, a standard error for the crossover contrast, or a confidence interval for that contrast.

As a general statistical point, a standard deviation is not a confidence interval. It describes variation among measurements rather than the precision of an estimated group comparison. In a crossover study, a paired analysis can use information about how measurements from the same participant move together. Marginal means and standard deviations alone do not reveal that within-participant relationship.

What does the sponsor’s t-test report?

The registry reports a one-sided t-test on the mean difference in final values for the primary analysis. The reported mean difference is 2.5, with p = 0.022. The analysis is categorized as non-inferiority or equivalence. A t-test evaluates a mean-based contrast under assumptions that depend on its design and implementation. The registry does not give enough detail to determine whether the test used paired differences appropriate to the crossover, how the direction was defined, or which non-inferiority or equivalence hypothesis and margin were prespecified.

In general, a non-inferiority test asks whether an intervention is not worse than a comparator by more than a prespecified margin. An equivalence test asks whether the difference lies within prespecified bounds in both directions. These are not interchangeable interpretations of a p-value. The margin and confidence interval are central to evaluating either claim. The registry does not report the margin, and the sponsor analysis’s confidence limits are not posted. Consequently, the p-value and the analysis label do not by themselves show whether the relevant criterion was met.

What is the recalculated rate comparison?

The recalculation treats AHI as an event rate and compares conventional ASV with modified ASV using a rate ratio. The recalculated estimate is 1.641, with an interval from 1.247 to 2.16 and p < 0.001. This is described as an unadjusted recalculation from posted summary statistics, not as the trial’s reported primary analysis. The calculation applies a Poisson model, which treats event counts as arising in relation to exposure time.

As a general statistical point, a Poisson model is most straightforward when counts are compatible with its assumptions, including an appropriate relationship between the mean and variance. Over-dispersion means the counts vary more than the model expects; if it is present and not accounted for, standard errors and resulting inference can be too optimistic. The posted summaries do not allow an assessment of the event-count distribution or over-dispersion. More fundamentally, the recalculation uses an assumed one-year exposure because the one-night timeframe could not be parsed. It therefore does not reproduce the stated endpoint’s actual exposure window. The recalculation also treats the arms as if their rates could be compared without the paired information of a crossover design.

The ratio’s orientation is conventional ASV relative to modified ASV. A ratio above 1 in that calculation indicates a higher rate assigned to the conventional group under the model. It does not estimate a within-participant treatment effect from the crossover data. Given the exposure mismatch, the modeling assumptions, and the discrepancy with the sponsor result, this recalculation is best read as a diagnostic comparison of posted summaries rather than a definitive analysis of the trial.

Why do the two analyses differ?

The sponsor reports a mean-difference t-test, whereas the recalculation uses a rate ratio and Poisson assumptions. They use different estimands and model structures, and the recalculation adds an assumed exposure duration not stated for the one-night endpoint. The sponsor analysis is the trial’s reported inferential analysis. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence; the recalculated result should not override it.

General statistical interpretation also depends on the analysis population, handling of missing values, endpoint definitions, and prespecified plan. Those details are not reported in the registry record. The result should therefore be described with its limitations rather than interpreted as if all analytic choices were known. The p-values are unadjusted, and the record does not explain whether or how multiple outcomes or analyses were considered in the original plan.

11. Confidence Intervals and Precision

A confidence interval gives a range of values compatible with the data and statistical model at the stated confidence level. In general, a narrower interval indicates greater precision, while a wider interval indicates greater uncertainty. Intervals should be interpreted in relation to the endpoint, the analysis method, and any clinically or scientifically meaningful threshold.

The sponsor’s reported primary analysis gives an 80% confidence level but does not report lower or upper confidence limits. The registry record therefore does not provide the interval needed to judge the precision of the reported mean difference of 2.5 or to assess it against a non-inferiority or equivalence margin. That margin is also not reported. The p-value, p = 0.022, does not convey the range of plausible mean differences.

The recalculated rate ratio is 1.641, with an interval from 1.247 to 2.16. This interval comes from the unadjusted Poisson recalculation, not the sponsor’s crossover analysis. Its numerical precision does not resolve the calculation’s limitations: the endpoint is stated as one night, whereas the recalculation uses an assumed one-year exposure; and the calculation does not account for paired observations. It should not be read as a confidence interval for the sponsor’s mean-difference analysis.

The posted standard deviations also show substantial spread in the endpoint measurements, particularly for conventional ASV. They are descriptive measures and cannot be substituted for confidence intervals around the crossover contrast. Without participant-level paired values, the analysis population, and the sponsor analysis’s confidence limits, the precision of the primary comparison cannot be fully assessed from the registry record.

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 based on the observed effect, not the trial’s original design assumptions. The registry record does not report the original sample-size justification. The planning calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The displayed figures are participants per arm, not total events.

For the primary AHI comparison, the planning illustration lists participants per arm for 80% power and participants per arm for 90% power at three assumed effect sizes: 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For example, planning for 75% of the observed effect gives 25 participants per arm for 80% power and 33 participants per arm for 90% power. These figures are not recommendations and do not describe the enrollment actually required under the trial’s original design.

In plain language, 80% power means that, if the assumed effect and planning assumptions were true, the design would have an 80% chance of detecting that effect at the stated significance level. The 90% power column represents a higher target chance under the same assumptions. Smaller effects require more participants: the illustration uses larger per-arm counts for 50% of the observed effect than for 75% or 100%. The plotted curve conveys that same general relationship across the chosen effect fractions.

This is not observed power. It is a prospective planning calculation using an effect estimated from the trial’s posted results, and it does not establish the probability that the trial result is true or that a treatment effect exists.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 3.9000; treatment rate λ₁ = 6.4000 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/3.9000 + 1/6.4000) / (1.00 × [ln(1.641)]²) = 13.2, rounded up to 14 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
lambda0 <- 3.9                      # control rate, events per patient-year
lambda1 <- 6.4                      # treatment rate
tt      <- 1                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(1405313)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 14 (80% power), 18 (90% power)
 75% of observed effect: n per arm = 25 (80% power), 33 (90% power)
 50% of observed effect: n per arm = 59 (80% power), 79 (90% power)
Simulated power, Poisson counts, n = 14 per arm: 0.833
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.660

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as a one-sided t-test on the mean difference in final values. It gives a mean difference of 2.5 and p = 0.022, and is labeled as a non-inferiority or equivalence analysis. The registry does not state the margin, identify which framework was intended, or report the confidence limits, so the result cannot be independently assessed against the criterion that would support either conclusion.

The recalculation is different: it estimates a conventional-to-modified rate ratio of 1.641, with an interval from 1.247 to 2.16 and p < 0.001. It treats the endpoints as rates under a Poisson model and uses an assumed one-year exposure, although the registry describes the endpoint timeframe as one night. It also does not account for the paired structure expected in a crossover trial. It is therefore not a replication of the sponsor’s analysis.

The record flags a discrepancy between the sponsor result and the recalculation. In that situation, the sponsor’s own analysis takes precedence as the trial’s reported inferential result. The recalculation is useful as a warning that an unadjusted summary-based method can yield a different result under different assumptions; it should not replace or be presented as confirmation of the sponsor’s analysis. The missing margin, confidence limits, and crossover-analysis details remain important limits on interpretation.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and one secondary endpoint. It gives an unadjusted p-value for each sponsor analysis, but does not report a multiplicity adjustment, a testing hierarchy, or a prespecified strategy for controlling the chance of false-positive findings across outcomes. As a general statistical point, when multiple hypotheses are tested, interpreting each unadjusted p-value as though it were the only test can overstate the strength of the overall evidence. The record does not establish whether the analyses were prespecified or how they were intended to support conclusions.

Missing-data methods and analysis populations are also not reported in the registry record. The posted arm summaries list 21 for each endpoint and arm, but the record does not explain whether these are all randomized participants, all participants with evaluable measurements, or another analysis set. It does not say whether any measurements were missing, how missing observations were handled, or whether any participants were excluded from the analyses. The existence or impact of missing data therefore cannot be assessed from the posted information.

These gaps matter in a crossover trial. General statistical practice requires attention to within-participant dependence and may also require assessment of period, sequence, or carryover effects, depending on the design and data. The registry confirms a crossover model but does not report sequence details, washout, or the methods used to address these issues. It also does not report whether the t-test was paired or how the analysis handled the design.

The sponsor analysis is labeled non-inferiority or equivalence, but the margin and confidence limits are absent. The registry record does not report a detailed statistical plan or interim-analysis information. These omissions prevent a complete evaluation of prespecification, multiplicity, and the relationship between the reported analysis and the trial’s intended decision criteria. They do not prove that the analyses were improperly conducted; they mean that those features cannot be verified from 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 serious adverse event terms

Serious events with the highest arm-level rate: diagnostic coronary angiogram (4.8%).

The adverse-event record lists one serious adverse event among 21 participants at risk in the conventional ASV group and none among 21 at risk in the modified ASV group. It lists no other adverse events in either group. Death counts are not reported in the registry record. The most frequently listed serious-event term is Diagnostic Coronary Angiogram, at 4.8%.

These are the posted event counts, not evidence that an intervention caused or prevented an event. The record does not give further information about event timing, relatedness to the device, severity criteria, or how the term Diagnostic Coronary Angiogram relates to the serious-event classification. With the information reported, the figures should be read as a brief description of events recorded in the registry, not as a comparative safety estimate.

In general, a small study and a limited observation period can provide little information about uncommon or longer-term adverse events. The registry describes the primary and secondary endpoints over one night, but does not provide a separate adverse-event observation timeframe. These safety figures cannot establish the absence of risk, and they should not be used alone to compare overall safety.

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

The posted results describe a randomized crossover comparison of modified and conventional ASV for periodic breathing, with one-night AHI as the primary endpoint. The group summaries show means of 3.9 events per hour for modified ASV and 6.4 events per hour for conventional ASV. The sponsor reports a one-sided t-test mean difference of 2.5 with p = 0.022 and labels the analysis as non-inferiority or equivalence.

Those details do not, on their own, establish non-inferiority or equivalence. The registry does not report the margin or the sponsor analysis’s confidence limits, which are necessary to evaluate the stated type of claim. The posted summaries also do not show paired participant-level results, and the registry does not explain how the crossover structure was incorporated in the sponsor analysis.

The separate recalculation gives a rate ratio and a small unadjusted p-value, but it relies on an assumed one-year exposure for an endpoint described as one night and does not use the crossover pairing. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence; the recalculation should not be used to overturn the reported sponsor result or to create a stronger conclusion.

The study’s measures are physiological indices collected over one night. The record does not report effects on symptoms, daily function, long-term outcomes, or other clinical endpoints. It also does not provide enough detail about participant selection, analysis populations, missing data, or the statistical plan to judge the robustness or generalizability of the results fully.

In general, statistical significance is not the same as clinical importance, and a lack of a reported statistically significant difference is not proof of equivalence. The registry results should be understood as reported measurements and analyses, with substantial limits on what can be concluded from them. They do not establish that either device is clinically beneficial, ineffective, or preferable.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of estimand and analysis method matters. The sponsor reports a mean-difference t-test in a randomized crossover study, while a separate calculation treating the posted summaries as event rates produces a rate ratio. These analyses do not answer precisely the same question. A summary-based rate calculation can appear statistically precise while failing to represent the paired comparison and exposure timeframe described for the trial.

The record also shows why a non-inferiority or equivalence label is not enough to interpret a result. The margin and confidence limits are central to these designs, yet they are not reported. A p-value by itself cannot establish that a difference falls within an acceptable range. Clear reporting of the estimand, analysis population, paired-data method, and decision margin would make the sponsor result easier to evaluate.

Finally, the case highlights the distinction between descriptive group summaries and inferential evidence. Means and standard deviations convey observed levels and variability, but not the precision of the within-participant treatment contrast. The record’s secondary endpoint points in the same direction as the primary summaries, but unadjusted secondary testing and unreported multiplicity planning limit how much additional weight it can carry.

These are broadly useful lessons for reading registry results: consider the design when interpreting a calculation, distinguish a trial’s reported analysis from a recalculation, and examine whether the reported precision matches the claim being made. The posted information supports a careful account of what was recorded, while leaving important analytic details unresolved.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

Several limitations are specific to this record. First, although the study is listed as a crossover, the posted summaries are group-level and do not provide paired measurements or the covariance between conditions. The registry does not state the sequence of treatment conditions, whether a washout was used, or how period and sequence effects were considered. These details are important for interpreting a within-participant comparison.

Second, the sponsor analysis is labeled as non-inferiority or equivalence, but its margin and confidence limits are not reported. The record gives a one-sided p-value without enough information to verify the decision criterion. It does not provide the detailed analysis plan, analysis population, or missing-data methods. It also does not report whether interim analyses were conducted.

Third, the summary-based recalculation does not align with the stated one-night timeframe: it uses an assumed one-year exposure. Its Poisson rate model does not represent the paired crossover comparison, and the posted summaries do not permit assessment of distributional assumptions or over-dispersion. The recalculation therefore has limited value as an estimate of the trial’s treatment contrast, particularly given the recorded discrepancy with the sponsor result.

Finally, both endpoints concern physiological events over one night. The registry does not report longer-term outcomes or patient-centered outcomes, and it gives limited information for interpreting the serious adverse-event listing. These reporting limits restrict assessment of precision, generalizability, and clinical importance. They should be treated as missing information in the registry record, rather than as evidence that the relevant methods or outcomes were absent from the full study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Modified Adaptive Servoventilation (ASV) Compared to Conventional ASV — NCT01405313.
• Registry record last updated 2017-03-20; status last verified 2012-09.
• Results first posted 2017-03-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, randomized, unmasked crossover study comparing modified ASV with conventional ASV in participants with periodic breathing. Enrollment is listed as 21, and ResMed is the sponsor. The primary endpoint is one-night AHI in events per hour; ODI is listed as a secondary endpoint.

The posted AHI means are 3.9 for modified ASV and 6.4 for conventional ASV. The sponsor reports a one-sided t-test mean difference of 2.5 with p = 0.022, categorized as non-inferiority or equivalence. The margin and confidence limits are not reported. A separate rate-based recalculation differs and uses an assumed exposure duration that does not match the one-night endpoint; the sponsor’s own analysis takes precedence.

The registry does not report important details about the crossover analysis, missing data, analysis populations, or multiplicity. The results are physiological measurements over one night and do not alone establish clinical benefit, equivalence, or comparative safety.