Choosing Options for Insomnia in Cancer Effectively (CHOICE): A Comparative Effectiveness Trial of Acupuncture and Cognitive Behavior Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Choosing Options for Insomnia in Cancer Effectively (CHOICE): A Comparative Effectiveness Trial of Acupuncture and Cognitive Behavior Therapy (NCT02356575), a randomized na study. The primary outcome is Insomnia Severity Index (ISI) at Baseline.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with no masking reported. The registry lists an enrollment of 160 and records 80 participants in the acupuncture group and 80 in the CBT-I group for the primary outcome. The study status is completed. Its start is recorded as 2015-02, and its primary completion as 2017-07. The phase is listed as not applicable.

The intervention schedules were not identical in format: acupuncture consisted of ten treatments over eight weeks, while CBT-I consisted of seven sessions over eight weeks. The posted results identify these as the two study arms. The registry summary says the investigators aimed to determine which treatment works better for insomnia in cancer survivors and also to study factors that might affect preference or response. Details of how those factors were measured or analyzed are not reported in the registry record.

The primary outcome entered in the record is baseline Insomnia Severity Index (ISI), reported as a mean and standard deviation. That timing matters for interpretation: baseline data describe the groups before the treatment period and are not a comparison of changes caused by treatment. Although the registry lists sleep-quality and sleep-diary outcomes, the posted primary result is not a follow-up treatment effect.

The record includes 38 outcome measures and indicates 35 secondary outcomes posted, but it reports no analyses. The original protocol’s statistical analysis plan, including the intended primary treatment-effect contrast and handling of missing data, is not reported in the registry record. Random allocation describes how participants were assigned, but by itself does not establish what analysis was planned or whether all randomized participants were included in the posted outcome summaries.

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.

6. Primary Endpoint

The registry lists the primary outcome as Insomnia Severity Index (ISI) at Baseline, measured over At Baseline.

The primary endpoint is the Insomnia Severity Index (ISI) at baseline, reported as a mean score with a standard deviation. The registry describes the ISI as a validated patient-reported measure intended to assess insomnia symptoms, associated distress, and effects on daytime functioning. It has seven items, each scored from 0 to 4, with higher scores indicating more severe insomnia symptoms; the maximum score is 28.

The record gives interpretive categories: scores from 0-7 indicate no clinically significant sleep difficulties, 8-14 indicate sleep difficulties warranting further investigation, and 15+ indicate clinically significant insomnia. These categories help explain the scale’s meaning, but the posted group averages do not show how individual participants were distributed across categories.

A baseline ISI is useful for describing the groups’ starting symptom severity. It can also show whether the recorded group averages were similar before treatment. It does not measure improvement, establish a treatment response, or determine which intervention was more effective. To answer those questions, a result comparing post-treatment scores or change from baseline would be needed; such a primary treatment-effect result is not reported in the registry record.

7. Results Posted in the Registry

• CBT-I Group: mean 18.50 versus 17.60 on control; difference 0.90 (95% CI -0.42 to 2.22), standardized effect d = 0.21; z-test p = 0.181.

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.

Pittsburgh Sleep Quality Index (PSQI) at Baseline

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • CBT-I Group: mean 12.10 versus 11.80 on control; difference 0.30 (95% CI -0.77 to 1.37), standardized effect d = 0.09; z-test p = 0.583.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CBT-I Group and the control. The interval gives the range of effects that remain compatible with the data.

The Consensus Sleep Diary (CSD) Baseline Sleep Onset

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • CBT-I Group: mean 47.10 versus 32.10 on control; difference 15.00 (95% CI -0.05 to 30.05), standardized effect d = 0.31; z-test p = 0.051.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CBT-I Group and the control. The interval gives the range of effects that remain compatible with the data.

The Consensus Sleep Diary (CSD) Minutes Wake After Sleep Onset at Baseline

• 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:
  • CBT-I Group: mean 53.60 versus 58.00 on control; difference -4.40 (95% CI -116.61 to 107.81), standardized effect d = -0.01; z-test p = 0.939.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CBT-I Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary measures address other aspects of sleep, including sleep quality and sleep-diary measures such as sleep onset and wake after sleep onset. The detailed results available in the registry record for these measures are baseline summaries. They describe starting values across different measurement scales; they do not establish improvement during treatment or persistence of change after treatment.

The overall pattern should therefore be read as additional characterization of participants at baseline, alongside the primary baseline ISI result. The secondary measures may provide context about sleep at study entry, but they do not turn the primary endpoint into a treatment comparison. Although the registry outcome listings include change-from-baseline and later time points for some measures, analyses for those outcomes are not reported in the registry record. The posted results consequently do not permit a broad conclusion about comparative treatment effects across sleep outcomes.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis. In general, examining many outcomes creates more opportunities for apparently notable results to arise by chance, especially when results are interpreted separately without accounting for multiplicity. The record does not report a multiplicity plan or analyses of the secondary outcomes. It is therefore not possible to determine whether the listed measures were confirmatory, exploratory, or analyzed according to a prespecified hierarchy.

Secondary measures can still be informative when their timing, units, analysis, and relationship to the primary question are clear. Here, the baseline timing is central: differences in baseline means are not evidence that one intervention changed sleep more than the other. The secondary findings should be treated as descriptive context rather than independent confirmation of comparative effectiveness.

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

• Pittsburgh Sleep Quality Index (PSQI) at Baseline
• Pittsburgh Sleep Quality Index (PSQI) Change From Baseline at 8 Weeks
• Pittsburgh Sleep Quality Index (PSQI) From Baseline at 20 Weeks
• The Consensus Sleep Diary (CSD) Baseline Sleep Onset
• The Consensus Sleep Diary (CSD) Sleep Onset Change From Baseline at Week 8
• The Consensus Sleep Diary (CSD) Sleep Onset Change From Baseline at Week 20
• The Consensus Sleep Diary (CSD) Minutes Wake After Sleep Onset at Baseline
• The Consensus Sleep Diary (CSD) Minutes Wake After Sleep Onset Change From Baseline at Week 8

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score on a scale, summarized by a mean and standard deviation. In general, a mean describes the average recorded score, while a standard deviation describes the spread of individual scores around that average. Neither summary by itself shows the full distribution of responses. For the ISI, a higher score represents more severe insomnia symptoms, according to the registry description.

What does the mean difference represent?

The comparison is expressed as the CBT-I group’s mean minus the acupuncture group’s mean. The reported estimate is 0.9 points. This direction means the posted baseline mean was higher in the CBT-I group. Because the outcome is measured at baseline, the contrast is about starting scores; it should not be interpreted as a difference in treatment effects. A mean difference summarizes the groups on the scale’s original units, which makes it more directly interpretable than a standardized effect measure.

What does an unadjusted comparison mean?

The posted comparison is an unadjusted recalculation from the group summaries. “Unadjusted” means it does not account for other variables, such as baseline characteristics, in a regression model. In general, adjustment can be useful when an analysis is designed to account for prognostic factors or to improve precision. The registry record does not report a model-based primary analysis, covariate adjustment, or the analysis plan. The recalculated contrast therefore should not be presented as the sponsor’s definitive inferential analysis.

Randomization and statistical adjustment are different features. Random allocation is a design method intended to reduce systematic differences between groups. Adjustment is an analysis choice that may account for measured variables. Neither feature changes the timing of this endpoint: a baseline score remains a starting measure rather than a post-treatment response.

How should the p-value be read?

The reported unadjusted p-value is 0.181. In general, a p-value describes how unusual data at least as incompatible with a specified no-difference model would be under that model and the assumptions used for the test. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The registry record does not report the sponsor’s testing procedure or broader analysis plan, so this p-value should be understood as part of the unadjusted summary-statistic comparison.

A p-value above a conventional threshold does not prove equality. Evidence about the range of plausible differences is better conveyed by the confidence interval alongside the estimate. For this comparison, the interval includes values on either side of no difference. That indicates uncertainty in the direction of the baseline contrast; it does not establish equivalence or answer a treatment-effect question.

Why does dispersion matter?

The standard deviations of the ISI scores are 4.1 in the acupuncture group and 4.4 in the CBT-I group. In general, variability affects the precision of a mean difference: greater spread among individual observations makes it harder to estimate a group mean precisely, all else equal. A group average can conceal variation in individual experiences, which is one reason a mean should not be treated as a description of every participant.

Other continuous measures in the registry have their own units and reported dispersion. In general, measurements with substantial variability can produce wide uncertainty around a group contrast. For the Consensus Sleep Diary sleep-onset measure, the posted group spreads are notably different, and the confidence interval for the difference is wide. This illustrates why a point estimate alone is not a sufficient account of a result. The registry identifies the wake-after-sleep-onset measure’s dispersion as a standard error, whereas the primary ISI dispersion is identified as a standard deviation; these quantities have different meanings and should not be treated as interchangeable.

What is and is not reported?

The record lists no analyses. It therefore does not report whether the original study used an intention-to-treat population, how missing observations were handled, whether baseline scores were used as covariates in follow-up analyses, or whether multiplicity was addressed. These omissions limit assessment of the planned inferential approach. General statistical interpretation can explain the summaries, but it cannot fill in methods that are not reported in the registry record.

The sample-size calculations are planning illustrations based on observed effects and stated assumptions, not the original trial’s design justification. Their interpretation is separate from the primary baseline comparison. They show how assumed effect size affects planning under the stated calculation approach; they do not demonstrate that the trial had a particular probability of detecting an effect.

11. Confidence Intervals and Precision

The estimated baseline mean difference in ISI is 0.9 points for CBT-I relative to acupuncture. Its confidence interval runs from -0.418 to 2.218. The lower limit is negative and the upper limit is positive, so the interval includes no difference and also permits differences in either direction. The endpoints are expressed to three decimal places. This range is more informative than the point estimate alone because it communicates the uncertainty around the estimated contrast.

In general, a confidence interval is a range produced by a statistical procedure that, under its assumptions and repeated use, has a specified coverage property. It is not a range containing a known proportion of individual participants’ scores, nor does it assign a probability to the true effect after the data are observed. The registry record does not report the sponsor’s analysis method or confidence-interval procedure, so the posted interval should be read in the context of the unadjusted summary-statistic comparison.

The interval is for a baseline difference, not a treatment effect. Its inclusion of zero does not prove the groups are equivalent, and its limits do not describe what either group experienced after treatment. Precision about the baseline contrast cannot compensate for the absence of a reported primary follow-up comparison. The result is compatible with a range of baseline differences, while leaving the comparative effectiveness question unanswered by this endpoint.

The secondary baseline intervals also vary in width. In general, wide intervals indicate that the estimate is imprecise, while narrow intervals indicate greater precision under the analysis assumptions. Intervals should be interpreted together with the outcome’s units, timing, and direction. In particular, the sleep-diary outcomes are measured in minutes and cannot be read on the ISI scale.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size planning figures are stated as participants per arm, not as total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect as a starting point, then consider planning for 100%, 75%, or 50% of that observed effect. The trial’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm under the calculation assumptions for an 80% chance of detecting the stated effect if that effect were the true one and the model assumptions held. The 90% power column uses a higher target chance under the same general interpretation. Power is a planning property tied to an assumed effect, design, variability, and testing procedure; it is not a guarantee that a study will detect an effect.

The planning figures increase as the assumed effect becomes smaller. This is expected in general: a smaller difference is harder to distinguish from random variation, so more participants are typically needed to achieve the same target power under otherwise unchanged assumptions. For example, planning for 75% or 50% of the observed effect requires larger per-arm figures than planning for 100% of that effect. The figures are illustrations based on the observed summaries, not evidence that the trial was originally designed around those assumptions. These calculations are not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.900; pooled standard deviation σ = 4.253.
2. n = 2 × (1.96 + 0.842)² × 4.253² / 0.900² = 350.5, rounded up to 351 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.899999999999999                      # observed difference in means
sigma <- 4.25264623499298                     # 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(2356575)
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 = 351 (80% power), 470 (90% power)
 75% of observed effect: n per arm = 624 (80% power), 835 (90% power)
 50% of observed effect: n per arm = 1,402 (80% power), 1,877 (90% power)
power.t.test: 351.4 
Simulated power at n = 351 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. Multiplicity, Missing Data and Analysis Populations

The registry record lists 38 outcome measures and indicates 35 secondary outcomes posted. The record reports no analyses. It does not describe a plan for controlling the risk of false-positive findings across multiple outcomes, time points, or comparisons. In general, testing many outcomes without an appropriate strategy can increase the chance that at least one result appears statistically notable by chance. A prespecified primary outcome and a clearly stated hierarchy can help readers distinguish confirmatory analyses from exploratory ones, but such a hierarchy is not reported in the registry record.

Missing-data handling is also not reported. The outcome summaries list 80 participants in each group for the primary endpoint, but this alone does not establish how missing observations were handled at follow-up, whether all randomized participants were analyzed, or whether any participants lacked outcome data. The registry record does not report imputation methods, sensitivity analyses, reasons for missingness, or outcome completion by time point. These details matter because analyses based only on observed measurements can be affected if missingness is related to participants’ outcomes or treatment experience.

The analysis population is not reported. The record does not state whether analyses followed intention-to-treat principles, used a per-protocol population, or applied another definition. It also does not describe adjustment for baseline values or other participant characteristics in follow-up comparisons. Such details cannot be inferred from random allocation or from the group summaries.

These omissions do not establish that the original trial lacked appropriate procedures; they mean that those procedures cannot be assessed from the registry record. The posted baseline summaries remain interpretable as descriptive statistics, but the absent analysis details limit evaluation of any intended confirmatory treatment-effect inference.

15. 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 non-serious adverse event terms

The registry records zero serious adverse events in the acupuncture group and zero in the CBT-I group, with 80 participants at risk in each group. It also records zero deaths in each group. These figures describe the serious-event and death counts entered in the registry; they do not establish that no events of any kind occurred.

Other adverse events are recorded for 10 participants in the acupuncture group and 5 in the CBT-I group. These are counts for the registry’s “other” adverse-event category, not serious adverse events. The record does not provide serious adverse-event terms, and it does not report detailed definitions, event timing, severity grading, relatedness assessments, or the duration of safety observation. Without those details, the counts cannot be interpreted as a full account of treatment tolerability or comparative safety.

Zero recorded serious events should be read as an absence of such events in the posted count, not proof that a risk is impossible. The registry figures are descriptive and do not by themselves establish a safety difference between groups.

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

The posted primary result supports a limited conclusion: the registry reports baseline ISI means of 17.6 for acupuncture and 18.5 for CBT-I, with a mean difference of 0.9 points and a confidence interval that includes no difference. The values describe the groups’ starting symptom scores. They do not show whether either group improved, whether improvement differed between treatments, or whether any change persisted.

The registry’s stated goal was to compare acupuncture with CBT-I for insomnia in cancer survivors and to investigate factors related to preference or response. However, the primary endpoint entered in the record is a baseline measurement. The registry also names follow-up and change outcomes, but does not report analyses for them. Thus, the available primary result does not resolve the comparative treatment question described in the study summary.

The absence of a reported statistically clear baseline difference is not evidence that the treatments are equivalent. Equivalence requires a suitable design and analysis with an explicitly defined margin; such an approach is not reported in the registry record. Nor does the baseline result establish that randomization produced identical groups on every characteristic. It only describes the recorded ISI means and the uncertainty around their contrast.

The ISI score categories offer context for the scale, but group means do not reveal how many individuals fell into each category. Similarly, the secondary baseline sleep measures provide additional descriptive information but do not substitute for treatment-related change estimates. The appropriate interpretation is therefore narrow: these posted data characterize baseline sleep-related outcomes and provide an uncertain baseline contrast, while the registry record does not report the analysis needed to assess comparative improvement.

17. Why This Trial Matters Statistically

This trial illustrates why outcome timing is as important as the outcome name. An insomnia severity scale may be relevant to a treatment question, but a score measured at baseline describes participants before treatment. It cannot directly show benefit, harm, or comparative change. Statistical interpretation must connect the estimate to the time point and contrast that generated it.

It also demonstrates the value of separating a study’s stated objective from the results actually reported in the registry. The summary describes a comparative-effectiveness aim, while the primary result available is a baseline mean. Recognizing that distinction prevents a descriptive baseline contrast from being mistaken for an estimate of treatment effectiveness.

Confidence intervals add useful context to a point estimate by showing a range of values compatible with the reported analysis. Here, the interval spans both directions around no difference. That matters because a non-significant p-value alone does not prove equality or communicate the full range of uncertainty. At the same time, precision cannot fix a mismatch between endpoint timing and the clinical question: a precise baseline comparison would still not be a treatment-effect estimate.

Finally, the record highlights how incomplete analysis reporting limits statistical assessment. Without reported analyses, multiplicity procedures, missing-data methods, or analysis-population definitions, readers cannot evaluate the intended inferential strategy. Registry summaries remain useful, but their scope should be respected: they support description of the posted measures, not conclusions that require unreported treatment comparisons.

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.

A central limitation of the available results is that the primary outcome is recorded at baseline, while the study’s stated purpose is to compare treatments. No primary post-treatment or change-from-baseline analysis is reported in the registry record. This limits direct evaluation of the comparative question.

The record reports no analyses and does not provide the original statistical analysis plan, sample-size justification, missing-data methods, or analysis-population definition. It also does not report whether or how secondary outcomes were adjusted for multiple comparisons. These omissions prevent assessment of whether the posted summaries align with prespecified analyses.

The trial was not masked according to the registry. In general, lack of masking can be relevant when outcomes are patient-reported, because expectations or awareness of assigned treatment may affect reporting. This is a methodological consideration, not evidence that reporting was biased in this trial. The registry does not provide details that would establish whether such effects occurred.

The treatment schedules differed in format: acupuncture involved ten treatments over eight weeks, whereas CBT-I involved seven sessions over eight weeks. The record does not report additional detail about intervention delivery, adherence, treatment fidelity, or participant preference results. Those features therefore cannot be assessed from the posted information.

The registry also does not report detailed eligibility criteria, follow-up completeness, or the reasons for missing outcomes. These limits mean that the baseline summaries offer only a partial view of the trial and should not be extended to unreported treatment effects or broader participant populations.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Choosing Options for Insomnia in Cancer Effectively (CHOICE): A Comparative Effectiveness Trial of Acupuncture and Cognitive Behavior Therapy — NCT02356575.
• Registry record last updated 2022-05-16; status last verified 2022-05.
• Results first posted 2019-10-02.
• 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

NCT02356575 is a completed randomized, parallel-group trial comparing acupuncture with CBT-I for insomnia in cancer survivors. The registry records enrollment of 160, with 80 participants in each arm for the primary baseline outcome. Treatment schedules were ten acupuncture treatments or seven CBT-I sessions over eight weeks; masking was listed as none.

The primary result is baseline ISI, reported as mean and standard deviation. The group means were 17.6 and 18.5, with an unadjusted mean difference of 0.9 and a confidence interval extending from -0.418 to 2.218. This is a baseline contrast, not a treatment-effect estimate. No analyses are reported in the registry record, and the original analysis plan and missing-data methods are not reported.