Naltrexone for Impulse Control Disorders in Parkinson's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Naltrexone for Impulse Control Disorders in Parkinson's Disease (NCT01052831), a randomized phase 4 study. The primary outcome is Percentage of Participants Assessed as Very Much Improved or Much Improved Based on the Clinical Global Impression-Improvement (CGI-I) Scale.

2. Clinical Question

The trial asked whether naltrexone was associated with a different pattern of improvement on the Clinical Global Impression-Improvement (CGI-I) scale than placebo among people with Parkinson’s disease and impulse control disorders. The registry’s brief summary describes participants as taking a dopamine agonist. The primary outcome defined a responder as someone assessed as very much improved or much improved on the CGI-I.

The registry lists the Questionnaire for Impulsive-Compulsive Disorders in Parkinson’s Disease Rating Scale (QUIP-RS) as a secondary outcome. The outcome information does not give additional results for that measure.

3. Trial Design

This was a randomized, double-blind, parallel-group, phase 4 study sponsored by the University of Pennsylvania. It is recorded as completed, with enrollment of 50. The registry lists 26 participants in the naltrexone arm and 24 in the placebo arm for the primary outcome. Randomization and double masking describe the intended comparative design; further details of the randomization process, concealment, or how masking was maintained are not reported in the registry record.

The active-treatment schedule began with naltrexone at 50mg per day for four weeks. Participants who were not in response at week 4 were increased to 100mg per day for the final four weeks. The placebo arm received a treatment described as looking identical to active study medication. The registry does not report additional details about dose changes, adherence, or treatment discontinuation.

The CGI-I was administered at Visit 2, described as week 2 and two weeks after baseline, and at Visit 5, described as the week 8 termination visit. The outcome description says a generalized estimating equation (GEE) model was used for change in response status over time. Details of the fitted model are not reported in the registry record.

The record lists two outcome measures and one secondary outcome. It reports no posted analyses in its analysis listing. Dates for study start and primary completion are recorded as 2009-11 and 2012-12. The original statistical design assumptions, including the intended sample-size justification, 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

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 Percentage of Participants Assessed as Very Much Improved or Much Improved Based on the Clinical Global Impression-Improvement (CGI-I) Scale, measured over The CGI-I was administered at Visit 2 (week 2, two weeks after baseline) and Visit 5 (week 8, termination visit 8 weeks after baseline)..

The primary endpoint is the percentage of participants assessed as much improved or very much improved on the Clinical Global Impression-Improvement scale. The CGI-I rates overall improvement on a seven-point scale, ranging from very much improved to very much worse. A rating of 1 or 2 qualifies as a responder; other ratings do not meet that responder definition.

This kind of endpoint reduces an ordered rating to a binary outcome: responder or not a responder. That makes the result interpretable as the share of participants who reached the specified level of global improvement, while omitting distinctions among the other scale ratings. The choice of responder threshold is important because it determines which ratings count toward the endpoint.

The registry states that CGI-I assessments were made at week 2 and week 8, and that a GEE model was used for change in response status over time. GEE is a general approach for estimating population-level associations when observations from the same participant may be related. The registry does not give the model’s exact specification or clarify how the posted arm percentages correspond to the assessments over time. The endpoint therefore should be read using the stated responder definition and the reported assessment schedule, without assuming additional details about the analysis.

7. Results Posted in the Registry

• Naltrexone: 53.8% (14/26) versus 33.3% (8/24) on control; risk difference 20.5 percentage points (95% CI -6.4 to 47.4), risk ratio 1.62 (0.83–3.15); unadjusted two-proportion z-test p = 0.144.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because each participant is classified as either a responder or not a responder using the CGI-I threshold. For a binary outcome, an arm-level percentage describes the proportion of participants who meet the defined event. Here, the event is a CGI-I rating of 1 or 2. The posted responder counts are 14 of 26 for naltrexone and 8 of 24 for placebo. The registry also gives arm-level percentages of 54.4% and 33.1%, respectively. Because the record describes a GEE analysis over time, those percentages should not automatically be assumed to be the same quantity as a simple proportion calculated from the counts.

A risk difference expresses the contrast between two event proportions on an absolute scale. A positive risk difference for the naltrexone comparison indicates a higher observed responder proportion in that arm than in placebo; a negative value would indicate a lower proportion. The unadjusted recalculation uses the posted responder counts and has an interval that includes values on both sides of no difference. The record does not supply enough model detail to treat that simple contrast as a reproduction of the stated GEE analysis.

A confidence interval describes the range of estimates that are reasonably compatible with the observed data under the method’s assumptions. Its width reflects precision: a wider interval represents greater uncertainty. When an interval for a difference includes the no-difference value, the data do not rule out no difference under that interval procedure. The interval does not show that every value in its range is equally likely, and it does not account for sources of bias that were not measured or modeled.

The reported p-value for the unadjusted recalculation is 0.144. In general, a p-value is calculated under a null model and summarizes how unusual data at least as inconsistent with that model would be. It is not a measure of effect size, nor a direct test of whether the trial was well conducted. The registry does not report an adjusted p-value for the GEE model in the analysis listing, so the recalculated p-value should not be presented as the complete result of that model.

The outcome description names generalized estimating equations for change in response status over time. In general, GEE methods account for the fact that repeated outcomes from the same participant may be correlated, and they commonly target an average association across the study population. This can be useful when participants are assessed more than once. The registry does not state the link function, working correlation structure, covariates, exact outcome coding over visits, or handling of missing assessments. Those details affect how the model is fitted and how its estimates should be interpreted.

In general, over-dispersion occurs when outcome variability is greater than assumed by a statistical model. If present and ignored, uncertainty estimates can be too small. The registry does not report whether over-dispersion was assessed or whether any adjustment for it was used. This is a general modeling consideration, not a finding about this study.

The distinction between an analysis specified in the outcome description and an analysis displayed in the record is important. The description says GEE was used, but the registry’s analysis listing reports no analyses. The record does not provide the GEE estimates, model-based uncertainty, or model diagnostics. The unadjusted recalculation is therefore a separate descriptive comparison based on the posted counts, not evidence that the GEE results have been reconstructed.

The planning figures are illustrations based on the observed effect, with the assumptions stated in the sample-size discussion. In general, sample-size planning asks how many participants would be required to detect a chosen effect under specified assumptions. Such projections depend on the event rates, effect size, significance level, allocation, and statistical method. They do not determine what happened in the enrolled sample. The registry’s original sample-size justification and design assumptions are not reported, so the illustration should not be confused with the trial’s original plan.

10. Confidence Intervals and Precision

The unadjusted risk-difference interval is broad and extends from a value favoring placebo to a value favoring naltrexone. This means the observed data do not pin down the direction or size of the difference with precision. The estimated difference is only a central summary; the interval makes clear that substantially different underlying effects remain compatible with the data.

Precision is influenced by the amount of information available and by the variability of the outcome. The primary comparison involves 26 participants in the naltrexone arm and 24 in the placebo arm, with 14 and 8 responders, respectively. With these group sizes, each participant’s classification can noticeably affect the estimated proportion. The width of the interval is therefore an important part of interpretation, rather than a technical detail to set aside.

The interval pertains to the unadjusted recalculation from counts. The registry’s outcome description instead states that GEE was used to assess change in response status over time. The model-based interval and estimate are not reported in the registry record, and the confidence level of the recalculated interval is not specified in the record. The unadjusted interval should not be treated as if it were the missing model-based result.

Intervals quantify sampling uncertainty under their statistical assumptions. They do not account for all possible limitations, including missing outcome data, deviations from the analysis plan, or limits on how broadly the participants represent the target population. Those issues require information that is not reported in the registry record. Taken together, the posted percentages give a descriptive contrast, while the broad interval calls for caution about the precision of any effect estimate.

11. 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, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 91 participants per arm for 80% power and 121 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 160 participants per arm for 80% power and 213 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 353 participants per arm for 80% power and 471 participants per arm for 90% power.

In plain terms, the 80% power column gives the planned participants per arm under the stated assumptions for a design with an 80% chance of detecting the chosen effect if that effect is present and the assumptions hold. The 90% power column describes the corresponding design with a higher planned chance of detection under those same assumptions. Smaller effects need more participants to detect, which is why the illustrations require larger groups as the target fraction of the observed effect becomes smaller.

These are planning illustrations, not observed power. They should not be interpreted as evidence that the completed trial had any particular probability of detecting an effect. The illustrations are based on the observed effect, and their assumptions may differ from those used in the original design.

12. 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 = 0.333; treatment proportion p₁ = 0.538; average p̄ = 0.436.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7013 = 1.3745.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6861 = 0.5774.
4. n = (1.3745 + 0.5774)² / (0.2051)² = 90.5, rounded up to 91 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 <- 0.333333333333333                          # control proportion
p1 <- 0.538461538461538                          # 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(1052831)
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 = 91 (80% power), 121 (90% power)
 75% of observed effect: n per arm = 160 (80% power), 213 (90% power)
 50% of observed effect: n per arm = 353 (80% power), 471 (90% power)
power.prop.test: 90.5 
Simulated power at n = 91 per arm: 0.797 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one secondary outcome, the QUIP-RS, and reports two outcome measures in total. The posted analysis listing contains no analyses. The record does not state whether a multiplicity adjustment was planned or used for the primary and secondary outcomes, or for comparisons across the repeated CGI-I assessments. Any adjustment strategy is therefore not reported in the registry record.

The outcome description identifies a GEE model for change in response status over time, but does not report the model estimates or enough detail to reconstruct the analysis. The exact handling of assessments at week 2 and week 8, the analysis population, and the model’s covariates and correlation assumptions are not reported. The record also does not state whether the primary result was based on all randomized participants, participants with available outcome assessments, or another defined group.

Missing-data methods and the number of participants with missing outcome observations at each visit are not reported in the registry record. Without that information, it is not possible to assess whether missing assessments differed between arms or how missingness may have affected the reported percentages and model. The record also does not report sensitivity analyses for missing data.

Interim analyses and any stopping rules are not reported in the registry record. The complete prespecified statistical analysis plan is also not reported, so the registry entry does not establish which analyses were planned in advance or whether all planned outcomes and analyses are displayed. These omissions limit assessment of multiplicity, analysis choices, and the robustness of the result; they do not by themselves establish that the study’s conduct or analysis was inadequate.

14. Safety Results

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

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports no serious adverse events among the 24 participants at risk in the naltrexone safety group and no serious adverse events among the 24 at risk in the placebo safety group. No serious adverse-event terms are listed. The record does not report deaths for these groups, so the death information is not reported in the registry record rather than establishing that no deaths occurred.

Other adverse events are recorded for 18 of 24 participants in the naltrexone group and 14 of 24 participants in the placebo group. These figures describe participants recorded as affected, not the total number of individual events. The registry entry does not give event names or further detail in the listed safety summary, so the figures do not describe severity, timing, duration, or whether an event was judged related to study medication.

Safety counts should be read as descriptive registry data. The absence of recorded serious events in these groups does not establish that serious events could not occur, and the group counts alone do not explain differences in exposure or follow-up. The available record does not provide additional safety-analysis methods or detailed adverse-event listings.

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

The registry records higher arm-level CGI-I responder percentages for naltrexone than for placebo: 54.4% and 33.1%, respectively. The posted counts are 14 of 26 and 8 of 24. The unadjusted recalculation has a p-value of 0.144, and its interval spans both directions of difference. The results therefore describe a numerical contrast but leave substantial uncertainty about the size and direction of the underlying difference.

The primary endpoint is a threshold-based measure of global improvement. It captures whether a participant was rated much improved or very much improved, rather than the full range of CGI-I ratings. In addition, the registry states that the outcome was assessed at week 2 and week 8 and that GEE was used for change over time. Since the model-based estimates and details are not reported, the posted unadjusted comparison cannot stand in for a full account of that longitudinal analysis.

These data do not establish that naltrexone works or does not work. A descriptive difference, a p-value, and an interval each answer different statistical questions, and none alone establishes a treatment conclusion. The wide uncertainty, limited group sizes, and missing details about the analysis and outcome completeness all matter to interpretation.

The result also does not establish what would happen in other populations or settings. The record describes a study of people with Parkinson’s disease and impulse control disorders, with the brief summary referring to dopamine-agonist use. More detailed eligibility information and the representativeness of enrolled participants are not reported. Conclusions should stay within the population and outcomes documented in the registry.

16. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition and analysis method both matter. The CGI-I responder measure has a clear threshold: ratings of 1 or 2 count as response. That makes the outcome easy to describe as a proportion, but it also discards distinctions between participants who did not cross the threshold. The reported percentages answer a specific binary question rather than describing every aspect of change on the underlying scale.

The study also highlights the distinction between a comparison of endpoint counts and an analysis of outcomes over time. The registry states that GEE was used for change in response status at repeated assessments. A simple count-based recalculation is useful for understanding the posted data, but it is not automatically equivalent to that model. When the model specification and estimates are absent, readers cannot verify how the repeated observations contributed to the primary result.

Finally, the point estimate and its precision must be considered together. The posted proportions differ, yet the count-based interval is broad and crosses the no-difference value. This contrast shows why a larger observed percentage in one arm is not, by itself, a precise estimate of a treatment difference. Reporting group sizes, responder counts, uncertainty, analysis details, and missing-data information is important for a balanced statistical reading.

The planning illustration adds another lesson: sample-size calculations depend on the effect one aims to detect and on assumptions about the design. The original design justification is not reported, while the registry’s illustration is based on the observed effect. Keeping those purposes separate prevents planning projections from being mistaken for evidence about the trial’s observed performance.

17. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations are evident from the registry entry. The primary outcome description mentions assessments at week 2 and week 8 and a GEE model, but model estimates and key specification details are not reported. The posted arm-level percentages and the count-based recalculation are not identical summaries, and the record does not explain how the percentages were obtained or how they relate to the model across visits.

The primary outcome groups are small, with 26 participants in the naltrexone arm and 24 in the placebo arm. The unadjusted interval is broad, limiting precision. Missing outcome counts by visit, missing-data methods, participant flow, and the analysis population are not reported in the registry record. These gaps prevent a detailed assessment of completeness and the effect of missing observations.

The registry does not report the original sample-size rationale, a full statistical analysis plan, multiplicity procedures, interim analyses, or stopping rules. Although one secondary outcome is listed, its results are not included in the registry record. The lack of these details limits evaluation of how fully the posted results reflect prespecified plans.

The safety summary records other adverse events for participants in both arms but does not provide event names or a detailed account of severity, timing, or attribution. Death information is not reported. Further demographic and eligibility detail is also not included in the registry record recorded for this analysis, so the breadth of application to other patient groups cannot be assessed from this entry alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Naltrexone for Impulse Control Disorders in Parkinson's Disease — NCT01052831.
• Registry record last updated 2015-08-06; status last verified 2015-07.
• Results first posted 2015-06-22.
• 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.

21. Record Summary

NCT01052831 is a completed, randomized, double-blind, parallel-group phase 4 study of naltrexone versus placebo for impulse control disorders in Parkinson’s disease. Enrollment was 50, with 26 participants in the naltrexone arm and 24 in the placebo arm for the primary outcome. Naltrexone began at 50mg per day, with an increase to 100mg per day for participants not in response at week 4.

The primary outcome was the percentage rated much improved or very much improved on the CGI-I, assessed at week 2 and week 8. The registry reports arm-level percentages of 54.4% for naltrexone and 33.1% for placebo and states that GEE was used to assess change in response over time. The unadjusted recalculation from counts has a p-value of 0.144 and broad uncertainty. Model details, missing-data methods, and the original sample-size justification are not reported in the registry record.