Study Assessing Effects of JZP-110 on Driving Performance in the Treatment of Excessive Sleepiness in OSA: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Assessing Effects of JZP-110 on Driving Performance in the Treatment of Excessive Sleepiness in OSA (NCT02806895), a randomized phase 2 study. The primary outcome is Standard Deviation of Lateral Position (SDLP) at 2 Hours Post-dose (Approximately at Tmax).

2. Clinical Question

3. Trial Design

The study was randomized, double-blind, placebo-controlled, and used a crossover model. It was listed as a phase 2 study and is marked completed in the registry record. Enrollment was 34. The recorded start date was 2016-07-05 and primary completion date was 2019-05-28. The registry lists obstructive sleep apnea and excessive sleepiness as conditions.

Participants received JZP-110 and placebo in treatment periods. JZP-110 dosing is described as 150 mg/day for the first 3 days and 300 mg/day for the next 4 days; placebo was described as once daily. The registry does not report the treatment sequence, period length beyond the stated dosing schedule, or any washout details. Those design features should not be inferred from the crossover label alone.

The primary endpoint was SDLP at 2 hours post-dose, described as approximately at Tmax. The posted primary groups include 34 subjects for JZP-110 and 33 for placebo. The record explains the difference: one subject participated only in Treatment Period 1 and did not receive placebo. For the 6-hour SDLP outcome, the posted groups each include 32 subjects. The registry does not explain the reduction in those analysis counts.

Driving took place on-road. Subjects were instructed to maintain a steady lateral position within the delineated boundaries of the slower right traffic lane while maintaining a constant speed of 95 kilometers per hour. The registry says vehicle speed and lateral distance to the left lane line were continuously recorded. Further details about randomization procedures, allocation concealment, analysis populations, and missing-data handling are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: One subject participated in only Treatment Period 1 and did not receive placebo resulting in 33 subjects in placebo group.

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 Standard Deviation of Lateral Position (SDLP) at 2 Hours Post-dose (Approximately at Tmax), measured over 2 hours post-dose.

The primary endpoint was standard deviation of lateral position, or SDLP, at 2 hours post-dose. It is a continuous measure of how much the vehicle’s lateral position varied while the driver attempted to maintain a steady position within the right traffic lane. The driving task also specified maintaining a constant speed of 95 kilometers per hour, with deviation recorded using vehicle speed and lateral distance to the left lane line.

SDLP is used to quantify lane-position variability during the driving task. The registry defines individual improvement as a decrease in SDLP below the negative value of a threshold. It defines individual impairment as an increase above the threshold or failure to complete the test because of sleepiness or subject-related safety concerns. These definitions explain how the study framed individual changes; they do not change the primary endpoint’s reported group-level continuous comparison.

The posted group values are least-squares means, with standard errors as the dispersion measure. The endpoint description identifies the assessment as occurring approximately at Tmax. The registry does not provide further detail about the derivation of the least-squares means or the model used to estimate them, aside from the reported ANOVA analysis. SDLP describes performance during this particular on-road test and time point; it is not, by itself, a measure of every aspect of driving or daily functioning.

7. Results Posted in the Registry

• JZP-110: mean 18.83 versus 19.92 on control; difference -1.09 (95% CI -2.83 to 0.65), standardized effect d = -0.30; z-test p = 0.220.

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.

SDLP at 6 Hours Post-dose

• 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:
  • JZP-110: mean 19.24 versus 20.04 on control; difference -0.80 (95% CI -2.55 to 0.95), standardized effect d = -0.22; z-test p = 0.370.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between JZP-110 and the control. The interval gives the range of effects that remain compatible with the data.

Standard Deviation of Speed (SDS) at 2 Hours Post-dose

• 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:
  • JZP-110: mean 2.62 versus 2.55 on control; difference 0.07 (95% CI -0.20 to 0.34), standardized effect d = 0.12; z-test p = 0.615.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between JZP-110 and the control. The interval gives the range of effects that remain compatible with the data.

SDS at 6 Hours Post-dose

• 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:
  • JZP-110: mean 2.73 versus 2.84 on control; difference -0.11 (95% CI -0.39 to 0.17), standardized effect d = -0.20; z-test p = 0.434.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between JZP-110 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover later SDLP, speed variability, and threshold-based counts for improved or impaired driving at several thresholds and assessment times. Across the posted continuous outcomes, the reported sponsor analyses do not all point in the same statistical direction: the secondary SDLP assessment at 6 hours has a reported p-value of 0.043, while the two reported SDS analyses have larger p-values. This broad pattern adds context to the primary endpoint but does not replace it.

The primary endpoint is SDLP at 2 hours post-dose, whereas the 6-hour SDLP measure addresses a different time point. SDS measures variability in speed rather than lateral position. Those outcomes are related to driving performance but are not interchangeable measures. The registry lists 26 secondary outcomes as posted, with 27 analyses in the record. A collection of outcomes can show mixed results even when a primary result is reported, particularly when measures differ in construct or timing.

Unadjusted secondary results carry less weight because examining many outcomes increases the chance that some results appear noteworthy by chance. In general, multiplicity procedures control the interpretation of repeated statistical tests, but the registry does not report whether any adjustment was used. The reported secondary p-values should therefore be read as individual results, not as a confirmed overall pattern of benefit or impairment. No single secondary finding resolves the discrepancy between the sponsor’s primary analysis and the unadjusted primary recalculation.

The registry also names threshold-based improved-or-impaired outcomes, but the listed secondary result details do not provide a single combined conclusion across those thresholds. Their interpretation depends on the particular threshold and assessment time. The results should be considered outcome by outcome rather than generalized beyond the recorded driving tests.

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

• SDLP at 6 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 1 Centimeter (cm) on JZP-110 Compared to Placebo 2 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 1.5 cm on JZP-110 Compared to Placebo 2 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 2.0 cm on JZP-110 Compared to Placebo 2 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 2.5 cm on JZP-110 Compared to Placebo 2 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 3.0 cm on JZP-110 Compared to Placebo 2 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 3.5 cm on JZP-110 Compared to Placebo 2 Hours Post-dose
• Number of Subjects With Improved or Impaired Driving at a Threshold 1.0 cm on JZP-110 Compared to Placebo 6 Hours Post-dose

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: SDLP is recorded in centimeters, and the posted arm values are least-squares means. A continuous outcome retains the magnitude of each measurement rather than reducing results to a simple improved/not-improved classification. The registry also describes individual improvement and impairment thresholds, but those threshold-based classifications are distinct from the primary group-level continuous outcome.

What does a mean difference represent?

In general, a mean difference expresses the contrast between the average outcome in two conditions, in the outcome’s original units. The recalculated primary contrast is -1.09 cm for JZP-110 relative to placebo, using the posted means. The negative direction reflects the lower posted mean for JZP-110. The registry’s endpoint definition associates a decrease in SDLP with individual improvement, but the recalculated contrast should not be treated as the sponsor’s model-based estimate.

The study used a crossover design, in which participants receive treatments in different periods. In general, crossover analyses can use within-participant information, while an unpaired comparison treats groups as if observations came from separate arms. The simple recalculation is an unadjusted summary-statistic comparison; it is not a reconstruction of the crossover ANOVA. The registry does not report enough model detail to reproduce that ANOVA or assess its treatment, period, or sequence terms.

What does the standard error describe?

The standard error describes uncertainty around an estimated mean, rather than the spread of individual observations. The primary arm standard errors are 0.63 for placebo and 0.627 for JZP-110. In general, a standard error depends on both variability and the amount of information contributing to the estimate. It should not be interpreted as the range of individual driving results. The registry lists standard error as the dispersion measure for the least-squares means.

The recalculation derives an approximate pooled standard deviation from the posted standard errors and group sizes. That approximation is used for the unadjusted effect-size and planning illustrations; it is not an observed standard deviation reported by the trial. The summary-statistic calculation also cannot account for the paired structure of crossover observations when the required participant-level data and model details are unavailable in the registry record.

How should the p-values be read?

In general, a p-value measures how incompatible the observed data are with a specified null model, under that model’s assumptions. It does not give the probability that the null hypothesis is true, and it does not measure clinical importance. The sponsor’s primary ANOVA reports p=0.006, whereas the unadjusted recalculation reports p=0.22. Because the record flags a discrepancy and the recalculation is not the sponsor’s crossover analysis, the sponsor’s analysis takes precedence for the trial’s reported inference.

The sponsor’s analyses are labeled superiority analyses. The registry does not report the detailed hypotheses, significance threshold for the original analysis, or full ANOVA specification. The general meaning of a p-value therefore does not supply missing information about the original analysis plan.

Why do modeling assumptions matter?

In general, model choice matters because it determines which features of the design and data contribute to an estimated contrast and its uncertainty. A crossover model may account for the repeated treatment periods, while a simple unadjusted calculation from group summaries does not reproduce those adjustments. The registry identifies the design as crossover and the sponsor method as ANOVA but does not report the model terms or diagnostics. Consequently, the summary-statistic calculation is best treated as a descriptive check, not as a competing reconstruction of the sponsor’s result.

Over-dispersion is a general concern when outcome variability exceeds what a chosen model assumes. It can make standard errors too small and confidence intervals too narrow if not handled appropriately. The registry record does not report a dispersion assessment or a correction for over-dispersion. This general point does not establish that over-dispersion occurred in this trial.

11. Confidence Intervals and Precision

The unadjusted recalculation gives a primary mean difference of -1.09 cm, with a 95% confidence interval from -2.832 to 0.652. In general, a confidence interval describes a range of values compatible with the data and the method used to calculate it. It conveys uncertainty about the estimated contrast; it is not a range containing a fixed proportion of individual driving measurements.

The recalculated interval includes zero, so this summary-statistic calculation does not distinguish the contrast from zero at the conventional level associated with a 95% interval. That statement applies only to the recalculation. The sponsor’s ANOVA reports a p-value of 0.006 for the primary analysis, and its estimate and confidence interval are not reported in the registry record. The sponsor’s model-based result and the unadjusted interval answer related but not identical statistical questions.

The interval’s width reflects limited precision in the simple recalculation. Its endpoints allow both a decrease and a small increase in mean SDLP under that calculation. The interval does not establish which values are practically important because the registry record does not report a threshold for a clinically meaningful group difference. Nor does the interval incorporate uncertainty about model selection, missing observations, or the suitability of the simple recalculation for crossover data.

More generally, precision depends on the information available and the assumptions of the analysis. The posted group sizes and standard errors give a basis for an approximate contrast, but participant-level paired data and full model output are not reported. The sponsor’s own confidence interval is not reported in the registry record, limiting direct assessment of the precision of its ANOVA estimate.

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 expressed as participants per arm for each stated power target, not as total event counts. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning illustrations based on the observed effect, not the original trial’s design assumptions, which are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column describes the corresponding planning target with a 90% chance. These are design calculations, not guarantees about a future study’s result. They are not observed power.

Rows using 100% of the observed effect plan around the full observed estimate; rows using 75% or 50% plan around smaller effects. Smaller effects require more participants to detect under the same assumptions, so the illustrative participant requirements increase as the assumed fraction declines. For example, the primary-endpoint illustration lists 175 participants per arm for 80% power at 100% of the observed effect, and 700 participants per arm at 50% of the observed effect. Those figures are not a recommendation or a reconstruction of the trial’s own enrollment rationale.

The illustrations use a two-arm equal-allocation normal approximation. The actual study is crossover, and its original sample-size justification and design assumptions are not reported in the registry record. The illustrations therefore should not be read as power calculations for the sponsor’s crossover ANOVA.

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 = -1.090; pooled standard deviation σ = 3.638.
2. n = 2 × (1.96 + 0.842)² × 3.638² / -1.090² = 174.9, rounded up to 175 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 <- -1.09                      # observed difference in means
sigma <- 3.63787160512636                     # 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(2806895)
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 = 175 (80% power), 235 (90% power)
 75% of observed effect: n per arm = 311 (80% power), 417 (90% power)
 50% of observed effect: n per arm = 700 (80% power), 937 (90% power)
power.t.test: 175.8 
Simulated power at n = 175 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary endpoint using ANOVA, labeled as a superiority analysis, with p=0.006. It does not report the ANOVA estimate, confidence limits, detailed model specification, or additional output needed to reproduce that analysis. The sponsor’s own analysis takes precedence because the registry flags a discrepancy between that result and the unadjusted recalculation.

The recalculated comparison uses the posted least-squares means and standard errors to form a simple unadjusted contrast. It gives a mean difference of -1.09 cm, a 95% confidence interval from -2.832 to 0.652, and p=0.22. This calculation is not the sponsor’s analysis and does not reproduce the crossover model. It is a summary-statistic re-analysis whose assumptions differ from the trial’s reported ANOVA.

The difference between the two p-values should not be resolved by selecting whichever value appears more persuasive. The sponsor’s analysis is the trial’s reported inferential result, while the recalculation indicates that a simple comparison of posted summaries gives a different conclusion. Without full model output or participant-level data, the registry does not permit a definitive reconciliation of the discrepancy. The reported p-value also does not provide the missing effect estimate or quantify its precision.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 27 outcome measures and 27 analyses, with 26 secondary outcomes posted. It does not report a multiplicity strategy, such as an adjustment across secondary comparisons, a testing hierarchy, or a prespecified order for interpreting outcomes. Without that information, the reported secondary p-values should not be treated as if each were the only statistical test conducted. Repeated testing can increase the chance of at least one apparently unusual result even when no true differences exist.

The registry identifies the sponsor’s primary analysis as ANOVA, but the full statistical analysis plan and model specification are not reported in the registry record. Details of the analysis population, treatment of period or sequence effects, and handling of repeated observations are also not reported. The record does note that one subject participated only in Treatment Period 1 and did not receive placebo, leaving 33 subjects in the primary placebo group. It does not describe how that participant’s available data entered the sponsor analysis.

For the 6-hour outcomes, the posted groups each include 32 subjects, but the reason those analysis counts differ from the primary counts is not reported in the registry record. The missing-data methods, including any imputation, exclusion rules, or sensitivity analyses, are not reported. It is therefore not possible to determine from the registry alone whether missing outcomes could have influenced the estimates or the reported analyses.

These omissions do not prove that the analyses were inappropriate. They limit the ability to independently assess how the sponsor handled multiplicity, incomplete treatment periods, and repeated measurements. The reported analysis and its discrepancy with the simple recalculation should be interpreted with those reporting limits in mind.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The serious adverse event figures report zero serious adverse events in the placebo group, where 33 were at risk, and zero in the JZP-110 group, where 34 were at risk. The registry also reports zero deaths in each group. These are counts for the recorded study groups; they do not establish that no serious events could occur outside the observed study period or in other populations.

For other adverse events, the registry reports 8 affected subjects among 33 at risk in the placebo group and 15 among 34 at risk in the JZP-110 group. These are descriptive counts, not evidence by themselves that a particular event was caused by treatment. The registry’s serious adverse event terms list is empty, so no serious-event terms are listed in the record.

Adverse-event counts depend on how events were defined, collected, and coded. Those details and the event-level descriptions are not reported in the registry record. The figures should therefore be read as the posted safety summaries, not as a complete characterization of safety or a causal comparison.

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

The posted primary means describe SDLP during a specified on-road driving assessment at 2 hours post-dose. The JZP-110 mean was lower than the placebo mean, and the sponsor reports a superiority ANOVA p-value of 0.006. The registry does not provide the sponsor’s estimated contrast or confidence interval, and the unadjusted recalculation produces a different inferential result. These points should be kept together when describing what the record shows.

The result does not establish how a particular person would perform, whether an observed difference is practically important, or whether it applies to driving outside the study conditions. The registry’s endpoint definition identifies lower SDLP as the direction of individual improvement, but the posted group comparison is not a personalized prediction. It also does not cover every dimension of driving performance or every time after dosing.

The trial’s crossover structure, its assessment at specified post-dose times, and the difference between the sponsor analysis and the simple recalculation all matter to interpretation. The registry does not report enough detail to reconstruct the sponsor’s model or resolve that discrepancy. Secondary results add information about other driving measures and times, but the multiplicity strategy is not reported, so they should be interpreted cautiously.

These findings describe a clinical trial record, not medical or driving advice. They do not establish a broad conclusion beyond the enrolled study population and recorded assessments. The record also does not report a clinically meaningful threshold for the group-level SDLP contrast, limiting interpretation of practical importance.

18. Why This Trial Matters Statistically

This trial is statistically notable because it used a randomized, double-blind crossover design for an on-road performance endpoint, while the registry reports only limited detail about the model used for its primary analysis. In crossover studies, within-participant comparisons can be informative, but the inferential result depends on how repeated treatment periods and other design features are handled. The registry names ANOVA but does not report the full model specification.

The primary result also illustrates why a p-value should not be read alone. The sponsor-reported analysis has p=0.006, whereas a simple unadjusted recalculation from posted summary statistics gives p=0.22 and a confidence interval that includes zero. The recalculation is not a substitute for the sponsor’s model, but the contrast shows why the estimate, uncertainty, design, and analysis method all matter. Because the discrepancy is flagged, the sponsor’s analysis takes precedence as the trial’s own reported analysis.

Secondary outcomes extend the assessment to other measures and times, but many comparisons make isolated p-values harder to interpret without a reported multiplicity plan. The registry also does not report missing-data methods or the original sample-size rationale. Those omissions limit independent assessment and illustrate the value of transparent reporting of analysis details, not just endpoint names and p-values.

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 trial-specific reporting limitations constrain interpretation. The sponsor’s primary ANOVA is reported as a superiority analysis, but its estimate, confidence interval, detailed model terms, and analysis population are not reported in the registry record. The discrepancy with the unadjusted recalculation cannot be reconciled from the posted information. The sponsor analysis takes precedence, but its precision cannot be evaluated from an unreported interval.

The simple recalculation uses posted summary statistics and does not reproduce the crossover analysis. Its approximate pooled standard deviation is derived from standard errors, and it does not use participant-level paired observations. Consequently, its confidence interval and p-value should not be treated as the sponsor’s model-based results.

The registry says one subject participated only in Treatment Period 1 and did not receive placebo. The reason for the 6-hour analysis counts of 32 in each group, missing-data handling, and sensitivity analyses are not reported. Treatment sequence, washout details, and period-level analysis details are also not reported in the registry record.

The multiplicity approach for the 26 posted secondary outcomes is not reported. The original sample-size justification and design assumptions are also not reported; the displayed planning illustrations are separate from the trial’s own design rationale. Finally, the registry does not report a threshold for a clinically meaningful group-level SDLP difference, limiting assessment of practical importance.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study Assessing Effects of JZP-110 on Driving Performance in the Treatment of Excessive Sleepiness in OSA — NCT02806895.
• Registry record last updated 2021-01-14; status last verified 2020-12.
• Results first posted 2020-06-16.
• 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

NCT02806895 is a completed, randomized, double-blind, placebo-controlled crossover phase 2 study of JZP-110 in people with excessive sleepiness due to obstructive sleep apnea. The primary outcome was SDLP at 2 hours post-dose. The registry reports a sponsor ANOVA p-value of 0.006, while the unadjusted recalculation differs; the sponsor’s analysis takes precedence. The registry does not report the sponsor’s primary estimate or confidence interval, full model details, multiplicity handling, or missing-data methods. Secondary outcomes include driving measures at 6 hours and measures of speed variability.