Efficacy, Safety and Tolerability of PF-06649751 in Parkinson's Disease Patients With Motor Fluctuations: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety and Tolerability of PF-06649751 in Parkinson's Disease Patients With Motor Fluctuations (NCT02687542), a randomized phase 2 study. The primary outcome is Change From Baseline in Daily OFF Time at Week 10.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-masked, placebo-controlled, dose-ranging Phase 2 study of PF-06649751 in people with Parkinson's disease who had motor fluctuations. The official title identifies a 15-week study. The registry lists enrollment of 108 and reports that the study was terminated. The reason for termination is not reported in the registry record.

Five treatment groups are listed: placebo and PF-06649751 at 1 mg QD, 3 mg QD, 7 mg QD, and 15 mg QD. The design therefore allows descriptive comparison across several dose levels, although the available posted analyses do not provide a sponsor estimate for every dose contrast. The primary endpoint was assessed at Week 10. The registry record gives a primary completion date of 2017-11-10 and a study start date of 2016-03-03.

Randomization can reduce systematic differences between groups at assignment, while masking is intended to limit knowledge of assigned treatment from influencing trial conduct or outcome assessment. The registry uses the term triple masking but does not identify which roles were masked. These design features do not remove uncertainty arising from the sizes of the analyzed groups, missing outcome measurements, or the analysis choices.

The primary efficacy analysis population was the Full Analysis Set, defined as randomized participants with at least one post-dose efficacy measurement from the Hauser home diary. The group sizes reported for the primary outcome differ across treatment arms. The registry does not explain the reasons for those analyzed group sizes or provide the original sample-size justification, planned interim analyses, or detailed original statistical plan. Its stated study purpose was to evaluate efficacy, safety, and tolerability.

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: Full Analysis Set consisted of all participants randomized who completed at least 1 post-dose efficacy measurement (Hauser home diary).

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 Change From Baseline in Daily OFF Time at Week 10, measured over Week 10; Baseline was defined as the average daily OFF time (using 3 Hauser patient diary days) prior to Day -1 (study derived day and equalled to nominal visit day 0)..

The primary endpoint was change from baseline in daily OFF time at Week 10, measured in hours. In Parkinson's disease, OFF time refers to diary-recorded time when the participant was in the OFF motor state. The registry says participants used a paper Hauser diary to record motor state in half-hour intervals. They completed diary entries for three consecutive days during the week before visits, with the stated exception of the Day 28 visit. Daily OFF time at a visit was calculated as the average of the three consecutive daily OFF-hour values.

Baseline was defined as the average daily OFF time from three Hauser diary days before Day -1, which the record describes as a study-derived day equivalent to nominal visit day 0. Expressing change from baseline gives a measure of how diary-recorded OFF time at follow-up compares with that baseline value. A negative group mean change indicates a reduction in OFF hours relative to baseline within that group; it is not, by itself, a comparison against placebo.

This endpoint is useful for a dose-ranging trial because it captures a daily motor-state outcome that can vary over time and can be summarized across diary days. The posted group values are least-squares means, with standard errors as the reported dispersion measure. Interpretation of the treatment contrast requires comparing groups, and the contrast remains subject to the uncertainty represented by its confidence interval.

7. Results Posted in the Registry

• PF-06649751 15 mg QD: mean -1.66 versus -0.97 on control; difference -0.69 (95% CI -1.86 to 0.47), standardized effect d = -0.28; z-test p = 0.242.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a continuous measure: daily OFF time in hours. A continuous outcome can take a range of values, so a group mean summarizes the central value while a measure of dispersion describes uncertainty or variability around that estimate. The registry reports least-squares means and standard errors. A least-squares mean is an estimate from a statistical model, and can differ from a simple arithmetic average if the model incorporates terms or adjustments. The model details for the primary endpoint are not reported in the registry record.

The posted group results include a least-squares mean change for placebo and for each PF-06649751 dose. The standard error describes the estimated precision of each group mean; it is not the same as the spread of individual participant outcomes. A smaller standard error generally indicates a more precisely estimated mean, while a larger one indicates more uncertainty. The standard errors are listed as the dispersion measure, and the registry record does not provide participant-level outcome data from which the underlying distribution can be examined.

The high-dose comparison can be expressed as the difference between the estimated mean change in the 15 mg QD group and the estimated mean change in placebo. The recalculated contrast is -0.694 hours. This is a simple unadjusted recalculation from the posted summary statistics, rather than the sponsor's model-based Bayesian dose-response estimate. The recalculated pooled standard deviation is marked as approximate, and the standardized effect estimate is -0.278. Such a standardized effect rescales a mean contrast relative to an estimate of outcome spread; it is not a direct measure in hours and depends on the variability estimate used.

The recalculated contrast also has a confidence interval from -1.857 to 0.469 and an unadjusted p-value of 0.242. A confidence interval expresses a range of values compatible with the data and the calculation method, under the method's assumptions. It shows uncertainty about the estimated contrast rather than a guarantee that the true value lies within the interval. The interval includes zero, which is the value representing no mean difference between groups under this contrast definition. The p-value is a summary of how incompatible the observed data are with a specified null model under the calculation's assumptions; it does not measure the probability that the null hypothesis is true.

In general, adjustment for multiple comparisons matters when investigators assess many doses, endpoints, or time points. Each additional inferential comparison can create more opportunities to observe an apparently unusual result by chance. Methods for handling multiplicity can preserve an overall error rate or use a structured testing strategy. Which approach was specified for this trial is not reported in the registry record. The reported recalculation is explicitly unadjusted, and should not be read as accounting for a family of comparisons.

The sponsor's posted result is identified as a Bayesian dose-response analysis. In general, Bayesian analyses combine the likelihood from the observed data with a prior distribution to produce a posterior estimate. The interpretation depends on the model, prior, and the way the reported interval and probability measures are defined. The registry record does not provide those details. It reports an estimate of -0.693, an interval from -1.713 to 0.304 at 90%, and a p value of 0.578. These should be reported as the sponsor's stated analysis rather than reinterpreted as if they were outputs of the unadjusted recalculation.

Over-dispersion is a general concern when observed variation is greater than assumed by a statistical model. If a model understates variability, uncertainty measures can be too narrow and inferential results can appear more certain than warranted. The registry record does not report an over-dispersion assessment for this endpoint, so no conclusion about it can be drawn for this trial. More generally, model fit, assumptions, handling of repeated diary measurements, and missing-data procedures affect how a model-based estimate should be interpreted.

The primary population was the Full Analysis Set, consisting of randomized participants who completed at least one post-dose efficacy measurement using the Hauser home diary. This definition is relevant because the endpoint depends on diary data after treatment began. The registry record does not detail how participants with some but not all diary days or visits were handled, whether imputation was used, or whether sensitivity analyses assessed departures from missing-data assumptions. It also does not report the original sample-size assumptions or a planned interim-analysis strategy.

10. Confidence Intervals and Precision

The recalculated placebo-versus-15 mg QD contrast is -0.694 hours, with a confidence interval from -1.857 to 0.469. The interval is wide enough to include a negative contrast and a positive contrast. Thus, the point estimate favors a more negative change in the high-dose group, but the range of values compatible with this unadjusted calculation also includes a contrast in the opposite direction. The data do not estimate the contrast with enough precision to settle its direction.

The interval's width is important because a point estimate alone can give a misleading impression of certainty. The posted estimate is one value derived from the data; the interval shows how much uncertainty remains around it under the calculation method. It does not mean that every value in the interval is equally likely, nor does it account for uncertainty from design or analysis choices that are not represented in the calculation.

The sponsor's Bayesian dose-response estimate is -0.693, with a 90% confidence interval from -1.713 to 0.304. That interval also spans zero and includes both negative and positive contrasts. Its interval is tied to the sponsor's Bayesian analysis, while the recalculated interval comes from the unadjusted summary-statistic comparison. The two intervals therefore describe different analyses, even though their point estimates are close.

The group standard errors and the unequal analyzed group sizes contribute to how precisely the group estimates and contrast can be determined. The registry record does not give the original precision target or a formal clinical threshold for interpreting a difference in daily OFF time. Consequently, statistical uncertainty can be described, but the clinical importance of a particular value within the interval cannot be established from the record alone.

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 expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total numbers across arms and are not total event counts. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The original sample-size assumptions for the trial itself are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 203 participants per arm for 80% power and 272 participants per arm for 90% power. Planning for 75% of the observed effect gives 361 participants per arm for 80% power and 483 participants per arm for 90% power. Planning for 50% of the observed effect gives 811 participants per arm for 80% power and 1,086 participants per arm for 90% power.

In plain terms, the 80% power column gives the modeled number of participants per arm for a future two-arm study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is present. The 90% column uses a higher target chance of detection, and therefore calls for more participants under the same assumptions. Smaller effects require more participants because they are harder to distinguish from random variation.

These are planning illustrations based on the observed contrast, not a retrospective measure of the trial's ability to detect an effect. They are not observed power. A future study's actual requirements could differ if its design, outcome variability, allocation, analysis, missingness, or target effect differs from these assumptions.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.694; pooled standard deviation σ = 2.494.
2. n = 2 × (1.96 + 0.842)² × 2.494² / -0.694² = 202.7, rounded up to 203 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 <- -0.694                      # observed difference in means
sigma <- 2.49379154568567                     # 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(2687542)
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 = 203 (80% power), 272 (90% power)
 75% of observed effect: n per arm = 361 (80% power), 483 (90% power)
 50% of observed effect: n per arm = 811 (80% power), 1,086 (90% power)
power.t.test: 203.7 
Simulated power at n = 203 per arm: 0.795 (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.

13. Analyses Reported by the Sponsor

The registry reports a sponsor analysis labeled Bayesian Dose Response Analysis for placebo and PF-06649751 15 mg QD. It gives an estimate of -0.693, a 90% confidence interval from -1.713 to 0.304, and a reported p value of 0.578. The estimate is close to the unadjusted recalculation of -0.694, but closeness of point estimates does not make the methods equivalent.

The recalculation uses posted summary statistics to form a simple unadjusted mean difference. The sponsor result is from a Bayesian dose-response analysis and may reflect a model and assumptions not described in the registry record. The record does not give enough detail to reproduce that analysis, assess its prior specification, or establish how its reported p value should be interpreted. The sponsor's interval is explicitly reported at 90%; the confidence level for the recalculated interval is not specified in the available record.

Both intervals include zero, and both cover values on either side of zero. They therefore convey uncertainty about the contrast's direction. The recalculated result is not a substitute for the sponsor's analysis, and the sponsor's analysis should be read according to its stated method rather than as a confirmation of the recalculation. The registry record does not report a discrepancy between the posted summary statistics and the sponsor estimate.

14. Multiplicity, Missing Data and Analysis Populations

The trial assessed a primary endpoint and a range of secondary outcomes. The secondary outcomes include changes in daily OFF time, daily ON time with troublesome dyskinesia, daily ON time without troublesome dyskinesia, MDS-UPDRS Part III, MDS-UPDRS Parts I, II, IV, and Total Score, as well as laboratory, vital-sign, and ECG summaries. Considering many outcomes, doses, or time points raises a general multiplicity concern: without an appropriate strategy, repeated testing can increase the chance of at least one apparently notable result arising by chance.

The registry record does not report the prespecified multiplicity strategy, if any, or whether the sponsor's analysis adjusted for multiple dose comparisons. The unadjusted recalculation should therefore be understood as a single contrast calculation, not as evidence that a broader family of comparisons has been controlled. The record also does not report a hierarchy of endpoint testing or a confirmatory testing plan.

The stated Full Analysis Set included randomized participants who completed at least one post-dose efficacy measurement using the Hauser home diary. This is the population definition attached to the primary endpoint. The registry record does not describe the number of missing diary entries or visits, the reasons for missing measurements, or the method used to handle incomplete diary data. It does not report whether all available diary days were used when a participant had fewer than the specified diary days, or whether imputation or sensitivity analyses were conducted.

These omissions matter because missing data can affect both the group estimates and their uncertainty, particularly when missingness is related to outcome or treatment. In general, analyses relying on assumptions about missingness should describe those assumptions and examine whether conclusions change under plausible alternatives. No such details are reported in the registry record, so the robustness of the primary analysis to missing data cannot be assessed from the posted information.

The record identifies the study as randomized and triple-masked, but does not report detailed allocation procedures, the roles masked, the full statistical analysis plan, or interim-analysis plans. It also does not report the original sample-size justification. These items limit assessment of how the posted analysis relates to the prespecified protocol and how fully the inferential results account for design decisions.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: nephrolithiasis (7.7%), ureterolithiasis (7.7%), pancreatic carcinoma (4.3%), neck pain (2.3%), pain in extremity (2.3%).

The serious adverse event counts are reported by group alongside the number at risk. Placebo had 1 affected participant among 23 at risk; the 1 mg QD group had 1 among 13; the 3 mg QD group had 0 among 15; the 7 mg QD group had 0 among 13; and the 15 mg QD group had 2 among 44. These are descriptive counts and denominators, not adjusted comparisons between groups.

The registry also reports deaths: 1 in the placebo group, none in the 1 mg QD, 3 mg QD, or 7 mg QD groups, and 1 in the 15 mg QD group. These counts do not establish whether an event was caused by study treatment. The record's listed serious-event terms include nephrolithiasis and ureterolithiasis at 7.7% each, pancreatic carcinoma at 4.3%, and neck pain, pain in extremity, and dermatitis allergic at 2.3% each. The registry information does not explain the denominator underlying each listed percentage in this summary.

Serious adverse events are distinct from the broader other-adverse-event counts. Those counts, like the serious-event figures, should be interpreted in light of the group sizes, follow-up, and event definitions. The registry record does not provide enough detail in this summary to make causal or comparative safety conclusions.

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

The posted primary results describe estimated changes in daily OFF time from baseline to Week 10. The estimated changes are negative in placebo and in each PF-06649751 dose group. For the placebo-versus-15 mg QD contrast, the recalculated mean difference is -0.694 hours. The estimate suggests a more negative change in the high-dose group relative to placebo, but the confidence interval from -1.857 to 0.469 includes no difference and values in either direction.

That combination of a point estimate and a wide interval means the observed data do not establish a precise treatment contrast. It would be inappropriate to treat the negative point estimate alone as proof of benefit, or to treat an interval that includes zero as proof that the groups are equivalent. The interval leaves room for effects of different magnitudes and directions under the calculation method. The sponsor's Bayesian result has a similar point estimate and also an interval spanning zero, but it comes from a distinct analysis.

Group changes from baseline should not be confused with randomized comparisons. The placebo group also had a negative estimated change, so the within-group reductions cannot be attributed to PF-06649751 by simply comparing each group with its own baseline. The between-group contrast is the relevant posted summary for assessing how the high-dose group differed from placebo, while still accounting for uncertainty.

The registry record reports that the trial was terminated, but the reason is not reported in the registry record. The termination status alone does not explain the endpoint estimates or establish why the study ended. The available information also does not provide the original design assumptions, missing-data methods, or complete multiplicity plan. These limitations prevent a full assessment of how the posted results fit within the trial's original analysis strategy.

Overall, the record supports a careful description of the estimates and their uncertainty, but not a definitive claim about efficacy, lack of efficacy, clinical importance, or causal safety. The findings apply to the trial population and analysis as recorded; broader conclusions require evidence beyond these posted summaries.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized design and a numerical point estimate are not enough to settle an efficacy question. The primary endpoint is a patient diary measure of daily OFF time, summarized as a least-squares mean change. Interpreting it requires distinguishing within-group change from the placebo-controlled contrast and then considering the uncertainty around that contrast.

The high-dose comparison is a useful example of how an estimate can be directionally suggestive while remaining imprecise. The recalculated difference is negative, but its confidence interval spans zero and extends into positive values. Reporting the interval alongside the estimate prevents the point estimate from being mistaken for a definitive result. The sponsor's Bayesian estimate is close numerically, yet it comes from a different method, demonstrating why method labels and assumptions matter even when estimates are similar.

The dose-ranging structure adds another statistical issue. A pattern across dose groups may be of interest, but a visual progression in group means is not equivalent to a tested dose-response relationship. Appropriate interpretation depends on the prespecified model and how comparisons across doses were handled. Those details are not reported in the registry record.

The planning illustrations also show why planning from an observed effect needs caution. Required sample sizes change substantially depending on the effect fraction selected, and the values rely on assumptions that may not match a future study or the original trial design. They are planning scenarios rather than evidence about the trial's observed power.

Finally, the endpoint depends on repeated diary measurement and the analysis population requires at least one post-dose efficacy measure. Missing-data handling and multiplicity decisions can therefore influence how results should be interpreted. This record highlights the value of reporting not only outcome estimates but also the methods and assumptions that determine their precision and context.

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.

The primary comparison's analyzed group sizes are uneven: the placebo estimate is based on 21 participants, while the 15 mg QD estimate is based on 41. The lower-dose groups have still smaller reported primary-outcome group sizes. The registry record does not explain why these group sizes differ or whether the differences reflect availability of diary measurements, exclusions, or another reason.

The recalculated confidence interval and p-value are unadjusted summary-statistic calculations. The pooled standard deviation is identified as approximate. These results are therefore useful as a transparent comparison from posted summaries, but they do not reproduce the sponsor's Bayesian dose-response model or account for any adjustments not specified in the registry record.

The record does not report the full model specification, the original statistical analysis plan, the original sample-size justification, the planned handling of missing diary data, or the multiplicity approach. It also does not provide a stated clinically important difference for daily OFF time. Without these details, it is difficult to judge whether the analysis followed prespecified decisions or to place the numerical contrast in a clinical-importance framework.

The study is listed as terminated, and the reason is not reported in the registry record. The primary analysis is at Week 10 within a study described as 15 weeks, and the available summary does not supply the full course of outcome results across the study period. The posted sponsor analysis focuses on placebo and 15 mg QD rather than reporting inferential estimates for every dose contrast. These features limit the conclusions that can be drawn from the primary summary alone.

Safety counts are also descriptive. The listed serious-event counts and deaths do not establish causation, and the record's abbreviated safety summary does not provide the clinical context needed to compare event profiles fully. The findings should be interpreted within these reporting and analysis limitations.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy, Safety and Tolerability of PF-06649751 in Parkinson's Disease Patients With Motor Fluctuations — NCT02687542.
• Registry record last updated 2020-11-23; status last verified 2020-10.
• Results first posted 2018-12-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a randomized, triple-masked, placebo-controlled, dose-ranging Phase 2 study of PF-06649751 in Parkinson's disease patients with motor fluctuations. The listed treatment groups are placebo and PF-06649751 at 1 mg QD, 3 mg QD, 7 mg QD, and 15 mg QD. Enrollment was 108, and the study status is terminated.

The primary endpoint was change from baseline in daily OFF time at Week 10, measured in hours with a Hauser diary. The posted group estimates are least-squares mean changes. For 15 mg QD versus placebo, the unadjusted recalculated mean difference is -0.694, with a confidence interval from -1.857 to 0.469 and p = 0.242. The sponsor's Bayesian analysis reports an estimate of -0.693 with a 90% confidence interval from -1.713 to 0.304 and a reported p value of 0.578.

Both analyses leave uncertainty about the direction and magnitude of the placebo-controlled contrast. The registry record does not report the reason for termination, the original sample-size justification, or key details of missing-data and multiplicity handling.