The Effect of Eszopiclone on the Arousal Threshold in Sleep Apnea Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effect of Eszopiclone on the Arousal Threshold in Sleep Apnea Syndrome (NCT01102270), a randomized early/phase 1 study. The primary outcome is Apnea Hypopnea Index.

2. Clinical Question

3. Trial Design

This was a randomized, triple-masked, crossover physiological study in obstructive sleep apnea. The registry lists an enrollment of 17 and describes eszopiclone and sugar-pill placebo as the treatment conditions. Each condition was described as being taken before sleep for one night. The study is classified as early phase 1 and is marked completed. Its listed start was 2009-01, and primary completion was 2009-08.

A crossover design compares treatments within a participant across different treatment periods, rather than assigning every participant to just one treatment for the entire study. That general feature can make within-person comparisons informative because a participant can serve as their own comparator. It also means that treatment order, timing between periods, and the analysis of paired observations matter. The registry record does not report the treatment sequence, any washout arrangements, or whether the posted statistical comparison accounted for the within-participant structure.

The outcome timeframe is an eight-hour in-laboratory polysomnogram. The primary outcome is the apnea-hypopnea index, and listed secondary outcomes include arousal threshold, nadir overnight oxygen saturation, and sleep duration. Numerical results are posted for oxygen saturation and sleep duration. A numerical arousal-threshold result is not reported in the registry record.

The registry identifies the sponsor as Brigham and Women’s Hospital. It does not report the original sample-size justification, recruitment details, eligibility criteria, participant flow, treatment-period details, or a full statistical analysis plan. Those omissions limit assessment of how the completed study followed its intended design.

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

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: although 28 were screened, only 17 were randomized since 11 did not qualify for the randomization portion of the study

6. Primary Endpoint

The registry lists the primary outcome as Apnea Hypopnea Index, measured over 8 hour In-Laboratory Polysomnogram (PSG).

The primary endpoint, the apnea-hypopnea index, counts respiratory events per hour of sleep. The registry describes respiratory events as lasting at least 10 seconds and being associated with a decrease in blood oxygenation or a cortical arousal from sleep. The endpoint therefore combines events involving reduced oxygenation and events associated with waking responses, scaled to time asleep.

This rate is used to summarize the frequency of breathing disturbances during sleep. It provides a standardized measure across sleep periods of different lengths, rather than simply counting all events without regard to how long the participant slept. The registry describes the result as a mean with standard error and specifies an eight-hour in-laboratory polysomnogram as the timeframe.

The endpoint relates directly to the study’s question about apnea severity, while arousal threshold is a proposed physiological mechanism that could influence respiratory events. The registry’s rationale focuses on whether changing the ease of arousal might alter the event rate for some participants. However, the primary endpoint alone does not establish that a change in event frequency occurred through a change in arousal threshold. A numerical result for that proposed mechanism is not reported in the registry record.

As with any sleep-study outcome, the result describes the measured laboratory period. The registry does not establish how these measurements relate to longer-term patterns or outcomes outside the study setting.

7. Results Posted in the Registry

• Sugar Pill: 31.00 versus 24.00 (events per hour of sleep) on control; rate ratio 1.29 (95% CI 1.14–1.47, 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.

Nadir Overnight Oxygen Saturation

• 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 errors.
• Result:
  • Sugar Pill: mean 80.00 versus 80.00 on control; difference 0.00 (95% CI -2.77 to 2.77), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sugar Pill and the control. The interval gives the range of effects that remain compatible with the data.

Sleep Duration

• 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 errors.
• Result:
  • Sugar Pill: mean 5.40 versus 6.80 on control; difference -1.40 (95% CI -2.28 to -0.52), standardized effect d = -1.07; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Sugar Pill than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes offer a mixed pattern rather than a uniform shift across all measured dimensions. The posted oxygen-saturation comparison shows no estimated mean difference, while the sleep-duration comparison points in a different direction from the oxygen result. This means the secondary measures do not all provide the same statistical signal as one another. The registry lists arousal threshold as a secondary outcome, but a numerical result for it is not reported in the registry record.

These outcomes relate to the primary result in different ways. Oxygen saturation and sleep duration describe aspects of the same laboratory sleep period, while arousal threshold concerns the proposed physiological pathway behind the study’s rationale. The secondary results can therefore add context, but they do not establish that the primary event-rate pattern occurred through the hypothesized mechanism. Without a posted arousal-threshold result, that pathway cannot be evaluated from the registry results.

The secondary comparisons are unadjusted. When several outcomes are examined, the chance of observing at least one apparently notable result can increase, even if each test is interpreted separately. General statistical explanation: adjustment for multiple comparisons can control that family-wise risk, while prespecified prioritization can clarify which findings are confirmatory and which are exploratory. The registry record does not report a multiplicity plan or identify a hierarchy among the secondary outcomes.

For that reason, the secondary evidence carries less weight than a prespecified primary analysis, particularly when the analysis plan and paired-data methods are not reported. These results are useful as descriptive information about the measured outcomes, but they should not be treated as independent confirmation of the primary finding.

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

• Arousal Threshold
• Nadir Overnight Oxygen Saturation
• Sleep Duration

9. Statistical Interpretation

10. Statistical Methods Explained

The statistics combine posted arm summaries with unadjusted calculations from those summaries. These methods can describe the size and uncertainty of a contrast, but they do not replace a complete analysis plan or resolve design details that the registry does not report.

What does an event rate mean?

For a rate outcome, the numerator is a count of events and the denominator is time at risk or exposure. Expressing events per unit of exposure allows rates to be compared even when the observed exposure differs. In this study, the primary endpoint is described as respiratory events per hour of sleep, and its stated timeframe is an eight-hour laboratory polysomnogram.

The posted arm summaries give mean event rates of 24 and 31 events per hour of sleep. The comparison calculation treats the outcome as a rate and uses a rate ratio. A rate ratio compares one condition’s rate with the other condition’s rate; a value of 1 would represent equal rates under that model. The reported estimate is 1.292 for sugar pill relative to eszopiclone. Its direction indicates that the estimated placebo rate is higher in the posted contrast.

The registry-derived comparison also lists event totals of 408 and 527. Those totals are inputs to a calculation, not independent participant counts. The rate calculation assumes a one-year exposure because the timeframe could not be parsed, although the endpoint itself is described as an eight-hour laboratory study. The registry record does not explain why that exposure was used. This difference between the stated study timeframe and the calculation assumption should be considered when interpreting the recalculated rate ratio and its uncertainty.

What does the Poisson assumption contribute?

A Poisson model is a common general approach for event counts, particularly when counts are related to exposure time. General statistical explanation: the model assumes events arise according to a rate, and its variance is linked to the expected event count. Over-dispersion occurs when the data vary more than that model expects. If over-dispersion is present and not accommodated, standard errors and confidence intervals may be too narrow. The registry-derived calculation is marked as Poisson-based; the registry record does not report an assessment of over-dispersion or an alternative count model.

This model choice concerns the distribution of counts. It does not, by itself, address the crossover design. In a crossover study, measurements from the same participant under different conditions are related. A paired analysis can account for that dependence. The registry record does not report whether the posted comparison incorporated within-person pairing, treatment order, or period effects. Without those details, it is not possible to confirm that the calculation reflects all features of the design.

How should the mean comparisons be read?

The posted secondary summaries report means and standard errors. A standard error describes uncertainty in an estimated mean; it is not the spread of individual observations. The recalculated mean differences use the posted summaries to form unadjusted contrasts. For nadir oxygen saturation, the posted means are both 80%, and the recalculated mean difference is 0.0 with an interval from -2.772 to 2.772 and an unadjusted p-value of 1.0. For sleep duration, the posted means are 6.8 and 5.4 hours, and the recalculated mean difference is -1.4 with an interval from -2.277 to -0.523 and an unadjusted p-value of 0.002. The comparison direction follows the listed eszopiclone and sugar-pill order.

These recalculations are unadjusted and based on summary statistics rather than participant-level records. They do not account for any unreported covariates or necessarily capture the paired structure. The registry record does not report the sponsor’s detailed analysis methods for these outcomes.

What does a confidence interval express?

In general, a confidence interval describes the range of estimates compatible with the observed data under the statistical model and its assumptions. A narrower interval indicates greater precision on that model’s scale; a wider interval indicates more uncertainty. The interval does not account automatically for bias, a mismatch between the model and the design, or outcomes and analyses that were not reported. A confidence interval also should not be read as a range containing all participant-level effects.

The primary rate-ratio interval is 1.135 to 1.47. The secondary intervals describe mean differences on their respective measurement scales. These are recalculated intervals from posted summary statistics; the registry record does not report a complete inferential analysis or any adjustment for multiple comparisons. Consequently, their interpretation is conditional on both the calculation and the unreported aspects of the analysis plan.

11. Confidence Intervals and Precision

The primary rate-ratio estimate is 1.292, with a confidence interval from 1.135 to 1.47. The interval lies on the higher-rate side of 1 under the reported contrast direction, which is sugar pill relative to eszopiclone. Its span reflects uncertainty in the recalculated estimate under the event-rate model. The unadjusted p-value is <0.001, but the p-value and interval do not address potential design-analysis mismatches.

The primary arm means are 24 and 31 events per hour of sleep, with standard errors of 4 and 5. Standard errors describe the precision of estimated means, not the range of participant-level AHI values. The registry does not post confidence limits for those arm means.

For secondary outcomes, the interval for nadir oxygen saturation extends from -2.772 to 2.772 for the mean difference, while the sleep-duration interval extends from -2.277 to -0.523. These recalculated intervals are unadjusted. Their widths should be interpreted on their own outcome scales, rather than compared directly with the primary rate-ratio interval.

Precision depends not only on sample size but also on outcome variability, the analysis model, and—in a crossover design—the handling of within-participant dependence. The registry record does not report the paired analysis details, a full analysis plan, or adjustments for multiple comparisons. Thus, the intervals quantify uncertainty under the calculations used, not all sources of uncertainty about the study’s interpretation.

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 are illustrations based on the observed effect, not the trial’s original design justification. For the primary event-rate outcome, the figures are participants per arm, not total events. The planning assumptions are two-sided significance level 0.05, equal allocation between two arms, and a normal approximation; the effect targeted is the stated fraction of the observed effect. The original trial’s sample-size assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 9 participants per arm for 80% power and 12 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 17 participants per arm for 80% power and 22 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 38 participants per arm for 80% power and 51 participants per arm for 90% power.

Power is the chance, under a specified statistical model and assumed effect, of detecting a difference at the chosen significance threshold. The 80% column describes a design intended to have an 80% chance of detecting the assumed effect; the 90% column describes a design intended to have a 90% chance. Smaller effects require more participants to achieve the same target power, which is why the planning figures increase as the assumed fraction of the observed effect decreases.

These values are not observed power. They are hypothetical planning calculations based on the observed effect and their stated assumptions. They do not show the power of the completed crossover study or establish that its original design used those assumptions.

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 = 24.0000; treatment rate λ₁ = 31.0000 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/24.0000 + 1/31.0000) / (1.00 × [ln(1.292)]²) = 8.9, rounded up to 9 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 <- 24                      # control rate, events per patient-year
lambda1 <- 31                      # 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(1102270)
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 = 9 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 17 (80% power), 22 (90% power)
 50% of observed effect: n per arm = 38 (80% power), 51 (90% power)
Simulated power, Poisson counts, n = 9 per arm: 0.814
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.638

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. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and several secondary outcomes, but it does not report how the analysis handled multiple comparisons. When several hypotheses are tested, interpreting every unadjusted p-value as if it were the only test can make false-positive findings more likely. General statistical approaches include adjusting significance thresholds, controlling an error rate across outcomes, or specifying in advance a hierarchy in which secondary outcomes are interpreted only after a primary result. The registry record does not say whether any such approach was planned or used.

The posted secondary comparisons are unadjusted. Their p-values should therefore be read as individual, exploratory evidence rather than as results with a reported family-wise multiplicity adjustment. The record also does not report a prespecified analysis hierarchy or identify which secondary results, if any, were intended to support confirmatory conclusions.

Missing-data handling is not reported in the registry record. There is no posted description of missing measurements, exclusions, incomplete treatment periods, or the method used to include participants with incomplete observations. In a crossover study, missing data in one treatment period can affect whether a within-participant comparison is possible, so this information would help assess the analysis.

The analysis populations are also not described. The registry does not report whether all randomized participants were included, whether participants were analyzed according to a particular treatment sequence, or whether any per-protocol or other population was defined. The enrollment count and arm summaries do not, on their own, identify the population used for every analysis.

Finally, the registry does not report whether the crossover comparisons accounted for treatment order, period effects, or within-person correlation. These omissions do not prove that such methods were absent; they mean that the registry record does not provide enough detail to evaluate them. Together, missing information about multiplicity, missing data, analysis populations, and crossover methods limits a full assessment of the reported inferential results.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry records zero participants affected by serious adverse events in each treatment group, with 17 at risk in each group. It also records zero participants affected by other adverse events in each group, again with 17 at risk. These figures describe the adverse-event counts entered in the registry for the recorded study period.

They should not be interpreted as proof that no adverse events of any kind occurred or that the treatments have no risks. The registry record does not provide event narratives, event severity beyond the serious-versus-other categories, timing, or a detailed account of how events were collected. Death counts are not reported in the registry record.

The study is small and describes one-night treatment periods in a laboratory setting. Adverse-event figures from this record therefore provide limited information about events in this study and do not characterize risks during longer or broader use. They are descriptive registry entries, not a comprehensive safety assessment.

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

The result describes a statistical contrast in an overnight laboratory measure among participants enrolled in a small crossover study. The posted primary summaries show a lower mean apnea-hypopnea event rate under eszopiclone than under sugar-pill placebo, and the recalculated unadjusted rate ratio and interval favor a higher rate in the placebo condition. This is a description of the posted data, not a conclusion about what any individual participant experienced.

The result does not establish that eszopiclone changes apnea severity through the proposed arousal-threshold mechanism. Although that mechanism motivated the study, a numerical arousal-threshold result is not reported in the registry record. Nor does the primary endpoint establish effects on outcomes beyond the laboratory sleep period. The record does not report longer-term measurements or broader clinical outcomes.

The result also does not settle how reproducible the contrast would be in other populations or study settings. Enrollment was 17, and the registry does not report detailed participant characteristics, eligibility criteria, or subgroup analyses. It therefore cannot show whether the observed pattern differs among participant types, including the group described in the study rationale as having a low respiratory arousal threshold.

Statistical interpretation has additional limits. The registry labels the design as crossover but does not describe the paired analysis, treatment order, or period handling. The recalculated rate comparison uses a one-year exposure assumption even though the endpoint timeframe is stated as an eight-hour laboratory polysomnogram. The analysis assumptions and this timeframe mismatch matter when judging the precision and relevance of the rate-ratio calculation.

In short, the posted data show a difference in the measured primary event rate between the two conditions under the reported comparison. They do not establish a mechanism, longer-term effect, or general result beyond this study, and they do not substitute for a complete analysis plan or participant-level data.

17. Why This Trial Matters Statistically

This study illustrates why statistical interpretation depends on more than the direction of group means or a small p-value. The primary endpoint is a rate, so its comparison relies on a model for event counts and exposure. The registry’s rate-ratio estimate is accompanied by an interval, but the calculation assumes a one-year exposure even though the stated endpoint timeframe is an eight-hour laboratory study. Recognizing that mismatch is important when interpreting the precision of a derived estimate.

The crossover label also highlights the role of design-aware analysis. Crossover comparisons can use within-participant information, but that requires attention to pairing and potentially to treatment order and period effects. The registry record does not report those analysis details. Readers should therefore distinguish the design description from evidence that the reported calculation accounted for every feature of that design.

The study also separates a physiological hypothesis from its measured primary outcome. The event-rate result addresses apnea-hypopnea frequency, while arousal threshold is the proposed mechanism. Without a numerical arousal-threshold result, the record cannot establish whether the hypothesized pathway changed alongside the primary endpoint.

Finally, the secondary outcomes and planning illustrations show why statistical results need context. Unadjusted secondary tests require caution when several outcomes are examined. Planning calculations based on an observed effect can help illustrate how sample size changes with the effect targeted, but they do not reveal the trial’s original design assumptions or its observed power. These distinctions are useful when reading small physiological studies and registry results more broadly.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

Several limitations specific to this study affect interpretation. Enrollment was 17, and the registry does not report participant characteristics, detailed eligibility criteria, or subgroup results. The study’s stated interest in people with a low respiratory arousal threshold therefore cannot be assessed for a defined subgroup from the posted data.

The treatment descriptions specify one night before sleep for each condition, and the primary measurement is an in-laboratory polysomnogram. The registry does not report the crossover sequence, timing between treatment periods, washout arrangements, or procedures intended to address possible period or order effects. It also does not report whether statistical comparisons accounted for paired observations.

The primary comparison has a specific measurement-timeframe concern: the outcome is described as events per hour during an eight-hour laboratory study, while the recalculated rate comparison uses an assumed one-year exposure because the timeframe could not be parsed. The registry record does not explain this assumption. The rate-ratio estimate and its interval should therefore be interpreted with that mismatch in mind.

The registry posts no numerical arousal-threshold result, despite that measure’s role in the study rationale. It also does not report a full statistical analysis plan, multiplicity handling, missing-data procedures, analysis populations, or the original sample-size justification. These omissions constrain evaluation of whether the posted analyses match the planned methods and how complete the outcome reporting is.

Finally, the safety entries are limited to registry counts, and death counts are not reported in the registry record. The available adverse-event information cannot characterize longer-term or broader safety outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Effect of Eszopiclone on the Arousal Threshold in Sleep Apnea Syndrome — NCT01102270.
• Registry record last updated 2017-04-18; status last verified 2017-04.
• Results first posted 2017-04-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, randomized, triple-masked, crossover early-phase study sponsored by Brigham and Women’s Hospital. It enrolled 17 participants with obstructive sleep apnea and compared one-night eszopiclone and sugar-pill conditions in an in-laboratory sleep study.

The primary outcome was apnea-hypopnea index, measured as respiratory events per hour of sleep. The posted arm means were 24 with eszopiclone and 31 with sugar-pill placebo. The recalculated unadjusted rate ratio was 1.292 for placebo relative to eszopiclone, with a confidence interval from 1.135 to 1.47 and p < 0.001.

Secondary results are posted for nadir overnight oxygen saturation and sleep duration. A numerical arousal-threshold result is not reported in the registry record. Details of crossover analysis, missing-data handling, multiplicity, and the original sample-size justification are also not reported.