Sleep Without Insomnia or The Use of Chronic Hypnotics: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Sleep Without Insomnia or The Use of Chronic Hypnotics (NCT03687086), a randomized na study. The primary outcome is Rates of Hypnotic Discontinuation.

2. Clinical Question

The clinical question is about reported medication discontinuation, not about sleep quality alone. The trial’s rationale notes that existing discontinuation programs may not sustain non-use for everyone and describes placebo-related expectations as another potential mechanism to address. The registry record says the programs differ in whether they address placebo effects, but does not map that distinction to Program A or Program B. Consequently, the outcome comparison can be described by program label, while attributing any difference to a specific mechanism is not supported by the posted details.

3. Trial Design

This was a randomized, single-masked, parallel-group trial. The registry lists an enrollment of 188 and a completed status. The phase is recorded as not applicable. The sponsor was the University of California, Los Angeles. The record lists sleep initiation and maintenance disorders as a condition.

The two arms were named Program A and Program B. Program A paired cognitive behavioral therapy type A with medications in packaging type A; Program B paired cognitive behavioral therapy type B with medications in packaging type B. The registry summary frames the comparison as a program that addresses placebo effects associated with hypnotic use versus one that does not. It does not specify which arm had which mechanism, nor does it give enough intervention detail to describe the therapy content or packaging beyond those labels.

The primary outcome was assessed 6 months after treatment ended, described as an average of 8 months after randomization. Its analysis population was narrower than the trial enrollment: participants had to complete that follow-up and provide medication-use data. The resulting analysis included 87 participants in Program A and 89 in Program B. The secondary measures with posted results used 92 participants in Program A and 96 in Program B and were assessed one week after intervention, an average of 9 weeks from randomization.

The registry record does not report the allocation ratio, masking procedures, treatment duration, the specific behavioral components, or the original sample-size justification. Details of the randomization process and the identity of the masked party are also not reported in the registry record. These omissions limit the extent to which the design can be reconstructed from the registry description alone.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: For this outcome, the analysis is performed only on those participants who completed the 6-month follow-up assessment and provided data on medication usage. As a result, there were 87 in program A and 89 in program B who met these criteria.

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 Rates of Hypnotic Discontinuation, measured over 6 months after treatment ends (which is an average of 8 months from randomization).

The primary endpoint was the number and percentage of participants who had stopped taking a benzodiazepine or z-drug at follow-up. Medication discontinuation was measured with 7-day self-reported medication logs. The assessment took place 6 months after treatment ended, an average of 8 months from randomization. For this outcome, only participants who completed the follow-up assessment and posted medication-use data were included: 87 in Program A and 89 in Program B.

This endpoint addresses whether participants reported current non-use within the medication-log period. It is therefore a binary outcome: each participant either met the discontinuation definition or did not. The registry describes this result as a count of participants and also calls it a percentage. It does not report an objective verification method, how incomplete logs were handled, or whether the definition required discontinuation of all hypnotics beyond the named benzodiazepine or z-drug categories.

Using medication discontinuation as the primary endpoint is aligned with the stated purpose of comparing programs designed to support stopping hypnotic medication. It differs from measuring symptom change: a participant’s sleep score and medication-use status are distinct outcomes, and one cannot be used as a substitute for the other. The registry record does not report whether the outcome definition or follow-up schedule was chosen on the basis of a formal protocol rationale.

7. Results Posted in the Registry

• Program B: 58.4% (52/89) versus 73.6% (64/87) on control; risk difference -15.1 percentage points (95% CI -28.9 to -1.3), risk ratio 0.79 (0.64–0.99); unadjusted two-proportion z-test p = 0.034.

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.

Insomnia Severity Index

• 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:
  • Program B: mean 6.47 versus 7.35 on control; difference -0.88 (95% CI -2.47 to 0.71), standardized effect d = -0.16; z-test p = 0.279.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Program B and the control. The interval gives the range of effects that remain compatible with the data.

Dysfunctional Beliefs and Attitudes About Sleep - Medication Subscale

• 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:
  • Program B: mean 2.72 versus 2.38 on control; difference 0.34 (95% CI -0.34 to 1.02), standardized effect d = 0.14; z-test p = 0.327.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Program B and the control. The interval gives the range of effects that remain compatible with the data.

Hypnotic 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:
  • Program B: mean 0.57 versus 0.40 on control; difference 0.17 (95% CI -0.27 to 0.61), standardized effect d = 0.11; z-test p = 0.452.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Program B and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes with posted numerical results cover three domains: insomnia severity, beliefs and attitudes about sleep medication, and hypnotic dose. They were assessed one week after intervention, an average of 9 weeks from randomization. Across these measures, the sponsor-reported intervals include the null value for a mean difference, and the reported p-values are above 0.05. The unadjusted calculations also do not show intervals excluding zero. Taken together, these secondary findings do not provide clear evidence of a between-program difference at that early assessment.

The primary outcome addresses a different question at a later follow-up: whether participants had stopped taking a benzodiazepine or z-drug at 6 months after treatment ended. The secondary measures are not interchangeable with medication discontinuation. An early sleep score or dose measurement may be related to later medication use, but the registry does not report an analysis testing that relationship. Thus, the secondary pattern neither establishes the mechanism for the primary result nor directly explains it.

The registry lists seven secondary outcome entries, with repeated entries for some named measures, while numerical results are posted for the three measure types at the stated post-intervention timeframe. The record lists 16 outcome measures and 8 analyses overall, but does not provide enough information to assess the full planned outcome and analysis structure.

Unadjusted secondary results carry less weight when many outcomes or comparisons may have been considered. General statistical explanation: testing multiple hypotheses increases the chance that at least one result appears unusual by chance, even if no individual effect is present. A prespecified hierarchy or multiplicity adjustment can address some of that concern, but the registry does not report whether either was used. The secondary findings should therefore be treated as supporting or exploratory context rather than as independent confirmation of the primary result.

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

• Insomnia Severity Index
• Insomnia Severity Index
• Dysfunctional Beliefs and Attitudes About Sleep - Medication Subscale
• Dysfunctional Beliefs and Attitudes About Sleep - Medication Subscale
• Rates of Hypnotic Discontinuation
• Hypnotic Dose
• Hypnotic Dose

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary outcome, each participant was classified according to whether the medication log indicated discontinuation. The posted counts are 64 of 87 for Program A and 52 of 89 for Program B. Because the outcome is binary, a comparison can be expressed using risks, a risk difference, a risk ratio, or an odds ratio. These measures describe the same underlying two-group data in different ways and have different interpretations.

What does a risk difference mean?

General statistical explanation: a risk difference subtracts one group’s event proportion from the other group’s event proportion. Its null value is zero, meaning no difference in the proportions. The recalculated risk difference is defined for Program B relative to Program A, so its negative direction indicates a lower observed discontinuation proportion in Program B in this analysis. The recalculated confidence interval lies below zero. This is an unadjusted comparison based on the posted summary counts, rather than a reproduction of the sponsor’s regression model.

A risk difference is expressed on the probability scale, which can be useful for understanding an absolute difference between groups. The registry also reports the two proportions used in the recalculation, but the four-decimal estimates are not repeated in this explanation. The risk difference does not itself adjust for other variables. Details of any adjustment in the sponsor’s logistic regression are not reported in the registry record.

How does the odds ratio differ?

General statistical explanation: an odds ratio compares the odds of an event between groups; odds are not the same as probabilities. An odds ratio of 1 represents equal odds under the comparison’s stated group ordering. The registry reports a logistic regression odds ratio of 1.95, a 95% confidence interval from 1.03 to 3.70, and p = .039. The group coding is not described in detail, but the direction is consistent with the sponsor’s interpretation of greater discontinuation odds for Program A than Program B. An odds ratio should not be read as a risk difference or as a direct percentage-point change.

For a binary outcome, the unadjusted risk difference and a regression odds ratio can differ in magnitude because they use different effect scales and may use different analysis specifications. The registry does not report enough model detail to determine whether the sponsor’s regression included covariates or other adjustments. The unadjusted recalculation is therefore a simple comparison from the posted counts, not a substitute for the sponsor’s analysis.

What do the continuous-outcome analyses estimate?

The posted secondary measures are means with standard errors: Insomnia Severity Index, the medication subscale of the Dysfunctional Beliefs and Attitudes About Sleep measure, and hypnotic dose in diazepam-equivalent milligrams. For each measure, the sponsor reports a mixed models analysis with a net mean difference, a 95% confidence interval, and a p-value. The record does not describe the model’s covariance structure, included terms, or handling of repeated measurements. The unadjusted recalculations compare the posted group summaries and are not the same as the mixed-model estimates.

General statistical explanation: a mean difference is the difference between group averages, and zero is the null value for a difference. A standard error describes the estimated sampling variability of a mean; it is not the same as the spread of individual participant scores. A mixed model can account for a structure in the observations, but the registry’s brief label does not reveal which structure or model specification was used. No more specific account of the sponsor’s approach is reported.

Why do the confidence intervals matter?

General statistical explanation: a confidence interval gives a range of estimates reasonably compatible with the data and the statistical procedure, under its assumptions. For a difference measure, an interval containing zero includes the null value; for an odds ratio, the corresponding null value is one. The primary sponsor-reported odds-ratio interval excludes one, while the posted secondary sponsor intervals include zero. Intervals describe uncertainty in estimates and should be considered alongside effect direction and scale, rather than replaced by a binary reading of p-values.

General statistical explanation: p-values depend on the null hypothesis, data, and model assumptions. They do not say how probable the null hypothesis is, and they do not quantify clinical importance. A small p-value is not a measure of the probability that a finding is due to chance. The registry does not report whether the analyses were prespecified in a statistical analysis plan, whether interim analyses were conducted, or whether any adjustment was applied for testing multiple outcomes.

11. Confidence Intervals and Precision

The primary recalculation gives an estimated risk difference for Program B relative to Program A with a confidence interval that remains below zero. This interval indicates that the observed difference is estimated with uncertainty, but that the range from the unadjusted calculation does not include zero. The associated unadjusted p-value is 0.034. The sponsor’s logistic regression reports an odds ratio of 1.95 with a 95% confidence interval from 1.03 to 3.70. That interval is above the odds-ratio null value of one, while still allowing a range of possible effect sizes.

These intervals answer different questions because one is on the risk-difference scale and the other on the odds-ratio scale. Their numerical endpoints cannot be compared directly. The registry does not report enough detail about the regression specification to explain any difference between the sponsor estimate and the simple recalculation beyond their different methods and measures.

For the secondary outcomes, sponsor-reported confidence intervals include the null value for each posted mean difference. The intervals are compatible with effects on either side of zero, and therefore do not pin down the direction of a between-program difference with high precision. The unadjusted recalculated intervals also include zero. This uncertainty means that the posted secondary results do not establish no difference; they indicate that the data do not sharply distinguish a difference from the null at those time points.

General statistical explanation: a confidence interval is a measure of statistical precision under a model and its assumptions. Narrower intervals indicate more precise estimation than wider intervals, but precision does not establish that an estimate is unbiased or clinically important. The intervals also do not capture uncertainty from unreported choices in outcome definition, missing-data handling, or model selection. The eligible primary analysis population was restricted to follow-up completers with medication data, and the registry does not explain how missing outcomes were handled. That limitation should be considered separately from the width of the reported intervals.

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 participants per arm for 80% power and participants per arm for 90% power. They are not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each calculation uses a stated fraction of the observed effect as the effect to detect. For the primary outcome, the illustration for 100% of the observed effect is 153 participants per arm for 80% power and 204 participants per arm for 90% power. The rows using 75% and 50% of the observed effect require larger participant counts.

In plain language, the 80% power column estimates how many participants per arm a hypothetical study would need to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real and the analysis assumptions hold. The 90% column makes the same kind of planning calculation for a higher target probability of detecting that effect. These percentages are design targets, not probabilities that the observed finding is true.

The sample-size illustrations are based on observed effects and are not the trial’s original design calculations. The original sample-size justification and design assumptions are not reported in the registry record. This is not observed power: observed power is not a useful retrospective measure of how convincing a result is, and the planning figures do not describe the probability that the trial’s result is correct.

Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants under the same assumptions. That pattern is reflected by the larger participant counts for planning around a smaller fraction of the observed effect. The figures are planning illustrations rather than a recommendation for a future study; actual planning would depend on a justified target effect, outcome definition, follow-up, analysis method, and anticipated missing data.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.736; treatment proportion p₁ = 0.584; average p̄ = 0.660.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6699 = 1.3131.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6613 = 0.5566.
4. n = (1.3131 + 0.5566)² / (-0.1514)² = 152.6, rounded up to 153 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
p0 <- 0.735632183908046                          # control proportion
p1 <- 0.584269662921348                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3687086)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 153 (80% power), 204 (90% power)
 75% of observed effect: n per arm = 265 (80% power), 354 (90% power)
 50% of observed effect: n per arm = 577 (80% power), 772 (90% power)
power.prop.test: 152.6 
Simulated power at n = 153 per arm: 0.804 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as logistic regression, with an odds ratio of 1.95, a 95% confidence interval from 1.03 to 3.70, and p = .039. The unadjusted recalculation from the posted counts instead uses a risk difference for Program B relative to Program A and gives p = 0.034. Both summaries point in the direction of higher discontinuation in Program A, but the effect estimates use different scales and the methods are not identical.

The registry does not describe the regression’s covariates, coding details, or other model specifications, so the reported odds ratio cannot be reconstructed from the record. The sponsor’s analysis is the trial’s reported analysis; the recalculation is a simple unadjusted analysis of the posted summary counts. Neither the difference in p-values nor the difference in effect measures should be treated as a contradiction. The registry does not flag a discrepancy between the reported and recalculated results.

For the secondary outcomes, sponsor-reported mixed-model analyses give net mean differences and 95% confidence intervals. Those estimates may differ from the simple unadjusted mean comparisons because the methods differ, and the record does not give enough model detail to explain the exact relationship. The sponsor-reported results are the analyses to use when describing the trial’s own statistical findings; recalculated results are useful as a transparent, limited comparison based on the posted summaries.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome analysis was restricted to participants who completed the 6-month follow-up and provided medication-use data. That means the posted primary comparison is not an analysis of every enrolled participant. The registry reports 87 participants in Program A and 89 in Program B for this endpoint, but does not state how many participants lacked follow-up, how many lacked usable medication logs, or why any data were unavailable.

The registry record does not report the method used to handle missing primary outcome data, such as imputation, weighting, or a sensitivity analysis. It also does not describe whether participants were analyzed according to their randomized assignments regardless of treatment participation. The posted secondary analyses use 92 participants in Program A and 96 in Program B, but the record does not explain why those analysis populations differ from the primary outcome populations or how missing secondary measurements were handled.

Multiplicity is also not described. The record lists 16 outcome measures and 8 analyses, and lists repeated entries for several secondary outcomes. It does not report a prespecified outcome hierarchy, an adjustment for multiple testing, or a statistical analysis plan that would clarify which tests were confirmatory and which were exploratory. Without that information, isolated secondary p-values should be interpreted cautiously, especially when several outcomes may have been examined.

The registry record does not report interim analyses, stopping rules, protocol deviations, or details of a sample-size justification. It also does not explain whether the primary outcome analysis was prespecified in the form presented. These are limits on what can be assessed from the registry record; they do not establish that any particular analysis choice was or was not made. The available information supports description of the posted analyses, but not a complete audit of their prespecification or missing-data assumptions.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalization for respiratory viral illness (1.1%), death from covid-19 (1.1%), diverticulitis (1.1%), small bowel obstruction (1.1%).

The registry reports serious adverse events among 92 participants at risk in Program A and 96 in Program B. Four serious adverse events were reported in Program A and none in Program B. The record also reports one death in Program A and none in Program B. Other adverse events were reported for 5 participants at risk in Program A and 6 in Program B. These are descriptive counts; the registry does not provide a statistical comparison of the event rates.

The listed serious-event terms include hospitalization for respiratory viral illness, death from COVID-19, diverticulitis, and small bowel obstruction, each reported at 1.1%. The registry does not establish that these events were caused by either program, nor does it provide a detailed assessment of relatedness or timing in the information summarized. A death is an important event to note, but the presence of an event in an arm does not by itself establish a causal relationship with the intervention.

These safety figures use the reported at-risk groups and should not be conflated with the smaller primary outcome analysis populations. They provide a limited description of events recorded in the registry, not a comprehensive safety comparison or a basis for conclusions about comparative risk.

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

The primary result describes reported discontinuation among participants who completed follow-up and posted medication-use data. In those analyzed groups, the posted counts were 64 of 87 in Program A and 52 of 89 in Program B. Both the registry’s logistic regression and the unadjusted recalculation point toward a higher observed discontinuation proportion in Program A, although they use different measures and methods.

This finding does not establish that one program is clinically superior in every respect, that the observed difference was caused by a particular program component, or that placebo-related expectations explain the result. The registry does not identify which program addresses placebo effects, and the two interventions differ in both therapy type and medication packaging. Without additional design and analysis details, the result cannot isolate the effect of one mechanism from the rest of the program.

The outcome is based on self-reported medication logs covering 7 days at a follow-up assessment. It should not be interpreted as objective verification of medication use over the entire period since treatment ended. The registry does not report how sustained discontinuation was established or how missing logs were handled. Nor does this endpoint by itself show whether participants’ sleep improved, whether medication was restarted later, or whether other health outcomes changed.

The secondary results concern early post-intervention scores and dose, not the later primary discontinuation assessment. Their confidence intervals include the null values and do not clearly distinguish a between-program difference from no difference. They do not prove equivalence or rule out effects of meaningful size.

Overall, the registry supports a cautious description of an observed difference in reported discontinuation in the analyzed follow-up groups. It does not, on its own, establish the mechanism, generalizability to people outside the trial, or the balance of longer-term benefits and harms. Those questions require information beyond the posted registry results.

18. Why This Trial Matters Statistically

This trial illustrates why outcome scale matters in clinical statistics. The primary endpoint is binary, so the same group data can be expressed as a risk difference or an odds ratio. The unadjusted recalculation and the sponsor’s logistic regression both describe the comparison, but their numerical estimates answer different statistical questions and should not be swapped or interpreted as though they share a scale.

It also shows why the analysis population belongs alongside an outcome estimate. The trial enrollment was 188, while the primary endpoint analysis included only participants who completed follow-up and provided medication-use data. The result therefore describes the eligible follow-up group. Without details on missingness and its handling, it is difficult to assess how closely that group reflects all randomized participants.

Timing and construct matter too. The primary endpoint concerns discontinuation several months after treatment ended, while the secondary outcomes with posted results were measured one week after intervention. A later behavioral outcome and earlier symptom or dose measures cannot be assumed to move together. Clear distinction between those measures prevents an early secondary result from being mistaken for an explanation of a later primary result.

Finally, registry reporting can support useful statistical interpretation while leaving important questions unresolved. The record supplies counts, model summaries, and safety event totals, but does not report detailed modeling choices, multiplicity handling, or the original sample-size justification. Recognizing those limits helps readers distinguish what the data directly describe from what would require protocol or publication-level detail.

19. Limitations

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

The primary endpoint relies on 7-day self-reported medication logs. The registry does not report an objective verification method, how missing logs were treated, or whether discontinuation had to be maintained throughout the interval after treatment. The outcome analysis includes only follow-up completers with medication-use data, and the record does not explain the consequences of excluding participants without those data.

The comparison is between two bundled programs. Each arm combines a cognitive behavioral therapy type with a medication packaging type, and the registry does not describe the specific content of either therapy or packaging. Although the study rationale contrasts a program addressing placebo effects with one that does not, the record does not identify which arm corresponds to each description. The observed contrast therefore cannot isolate which program element, if any, accounts for the difference.

The primary follow-up is described as 6 months after treatment ended, averaging 8 months from randomization. The registry does not provide the distribution of actual follow-up timing, nor does it state whether the result reflects sustained discontinuation beyond the medication-log period. Generalizability is also difficult to assess because detailed eligibility criteria and participant characteristics are not reported in the record.

The sponsor’s regression specification and the mixed-model specifications for secondary outcomes are not described beyond their method labels. Missing-data procedures, multiplicity handling, interim analyses, and the original sample-size justification are not reported in the registry record. These gaps limit independent assessment of model assumptions and the confirmatory status of secondary findings. The safety information is also presented as event counts without a reported comparative analysis or detailed event-relatedness assessment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Sleep Without Insomnia or The Use of Chronic Hypnotics — NCT03687086.
• Registry record last updated 2026-04-07; status last verified 2024-12.
• Results first posted 2024-12-30.
• 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, single-masked, parallel-group trial sponsored by the University of California, Los Angeles, with enrollment of 188. It compared two programs combining different cognitive behavioral therapy types and medication packaging types. The stated primary outcome was discontinuation of a benzodiazepine or z-drug, assessed by 7-day self-reported medication logs at 6 months after treatment ended.

Among participants completing follow-up and providing medication-use data, the registry reports 64 of 87 in Program A and 52 of 89 in Program B as having stopped medication. The sponsor’s logistic regression reported an odds ratio of 1.95, a 95% confidence interval from 1.03 to 3.70, and p = .039. The unadjusted recalculation points in the same direction but uses a risk difference and a different method.

Posted secondary analyses concern insomnia severity, medication-related sleep beliefs, and hypnotic dose one week after intervention. Their reported intervals include the null value. The registry record does not report detailed missing-data procedures, multiplicity handling, or the original sample-size justification.