Evaluating the Efficacy, Safety, Pharmacokinetics, and Pharmacodynamics of BIIB054 in Participants With Parkinson's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluating the Efficacy, Safety, Pharmacokinetics, and Pharmacodynamics of BIIB054 in Participants With Parkinson's Disease (NCT03318523), a randomized phase 2 study. The primary outcome is Change From Baseline in Movement Disorder Society Sponsored Revision of the Unified Parkinson's Disease Rating Scale (MDS-UPDRS) Total Score (Sum of Parts I, II, and III) at Week 52.

2. Clinical Question

3. Trial Design

The registry record describes a multicenter, randomized, double-blind, placebo-controlled phase 2 study, with an active-treatment dose-blinded period. The design was parallel-group, and masking was recorded as quadruple. Enrollment was 357. The study began on 2018-01-10, had primary completion on 2020-10-26, and its current status is terminated.

During Year 1, the placebo group received matching placebo on Day 1 and every 4 weeks. The three early-start groups received BIIB054 at 250 mg, 1250 mg, or 3500 mg by intravenous infusion on Day 1 and every 4 weeks. In Year 2, participants who received placebo in Year 1 were randomized to an active-treatment arm and began BIIB054 at Week 52, with subsequent infusions every 4 weeks. The record therefore distinguishes early-start and delayed-start treatment histories; the primary Week 52 comparison is among placebo and early-start dose groups.

The primary outcome was change from baseline in MDS-UPDRS Total Score at Week 52. Posted arm summaries include 53 participants for placebo, 29 for 250 mg, 57 for 1250 mg, and 51 for 3500 mg. The primary population is defined in the registry as randomized participants who received at least one dose, while the analyzed numbers are outcome-specific. The registry record does not report why the study was terminated, the reasons participants did not contribute to a particular analysis, or the original design assumptions used to choose enrollment.

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.

Before assignment: Participants with Parkinson's Disease (PD) were enrolled and randomized to receive placebo or BIIB054 250/1250/3500 milligrams (mg) for Year 1 in Placebo-Controlled (PC) Period. Following Year 1, participants on placebo (delayed start) were re-randomized to receive BIIB054 250/1250/3500 mg dose, and others on BIIB054 in Year 1 continued to receive the same dose until their Week 96 visit.

Only the first 6 of 10 groups are shown.

PC Period: Up to Year 1

Reasons for not completing this period:

DBE Period:Year 2 to EOS (Up to 3 Years)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population was defined as all randomized participants who received at least one dose of study treatment (BIIB054 or placebo). Number of participants analyzed were participants analyzed for this outcome measure.

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.

Population: Intent-to-treat (ITT) population was defined as all randomized participants who received at least one dose of study treatment (BIIB054 or placebo).

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Movement Disorder Society Sponsored Revision of the Unified Parkinson's Disease Rating Scale (MDS-UPDRS) Total Score (Sum of Parts I, II, and III) at Week 52, measured over Baseline, Week 52.

The primary endpoint is change from baseline to Week 52 in the MDS-UPDRS Total Score, the sum of Parts I, II, and III. Part I covers non-motor experiences of daily living, Part II covers motor experiences of daily living, and Part III assesses motor signs. Parts I and II include participant-reported assessments, while Part III is administered by a rater. The total score ranges from 0 to 236, and a higher score indicates more severe symptoms of Parkinson's disease.

This composite measure brings several aspects of symptoms and daily functioning into one continuous outcome. A change score compares each participant's score at follow-up with their baseline score; the reported arm means are adjusted means. Such an endpoint can describe the direction and size of average change over the study period, while the between-group estimate addresses how the average change differs between a BIIB054 dose group and placebo.

The endpoint is relevant to the study's stated objective of evaluating clinical efficacy through dose response. However, the posted primary comparisons are separate dose-versus-placebo estimates at Week 52. They do not, by themselves, test every possible dose-response pattern or establish that observed changes are attributable to treatment rather than other influences.

7. Results Posted in the Registry

• PC Period: BIIB054 250 mg (Early Start): mean 10.48 versus 10.78 on control; difference -0.30 (95% CI -5.11 to 4.51), standardized effect d = -0.03; z-test p = 0.903.
• PC Period: BIIB054 1250 mg (Early Start): mean 11.29 versus 10.78 on control; difference 0.51 (95% CI -3.56 to 4.58), standardized effect d = 0.05; z-test p = 0.806.
• PC Period: BIIB054 3500 mg (Early Start): mean 10.86 versus 10.78 on control; difference 0.08 (95% CI -4.09 to 4.25), standardized effect d = 0.01; z-test p = 0.970.

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.

Change From Baseline in MDS-UPDRS Total Score (Sum of Parts I, II, and III) at Week 96

• 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:
  • PC Period: Early Start BIIB054 250 mg: mean 8.28 versus 7.88 on control; difference 0.40 (95% CI -5.14 to 5.94), standardized effect d = 0.03; z-test p = 0.887.
  • PC Period: Early Start BIIB054 1250 mg: mean 8.71 versus 7.88 on control; difference 0.83 (95% CI -3.67 to 5.33), standardized effect d = 0.06; z-test p = 0.717.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PC Period: Early Start BIIB054 250 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PC Period: Early Start BIIB054 1250 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in MDS-UPDRS Subpart I Score at Week 52

• 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:
  • PC Period: BIIB054 250 mg (Early Start): mean 0.90 versus 1.43 on control; difference -0.53 (95% CI -1.94 to 0.88), standardized effect d = -0.17; z-test p = 0.460.
  • PC Period: BIIB054 1250 mg (Early Start): mean 1.56 versus 1.43 on control; difference 0.13 (95% CI -1.06 to 1.32), standardized effect d = 0.04; z-test p = 0.831.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PC Period: BIIB054 250 mg (Early Start) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PC Period: BIIB054 1250 mg (Early Start) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in MDS-UPDRS Subpart II Score at Week 52

• 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:
  • PC Period: BIIB054 250 mg (Early Start): mean 2.72 versus 3.17 on control; difference -0.45 (95% CI -1.98 to 1.08), standardized effect d = -0.13; z-test p = 0.564.
  • PC Period: BIIB054 1250 mg (Early Start): mean 3.16 versus 3.17 on control; difference -0.01 (95% CI -1.30 to 1.28), standardized effect d = -0.00; z-test p = 0.988.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PC Period: BIIB054 250 mg (Early Start) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PC Period: BIIB054 1250 mg (Early Start) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 13 posted secondary outcome measures. These include the Week 96 MDS-UPDRS Total Score, changes in MDS-UPDRS subparts at specified follow-up visits, adverse events, serum concentration, pharmacokinetic and pharmacodynamic outcomes, and immunogenicity-related objectives. The detailed posted measures do not all have the same role: some describe clinical scores, while others concern safety or drug exposure.

Across the posted continuous score outcomes, the overall pattern is not a clear separation of early-start BIIB054 groups from their comparators. The available sponsor-reported Week 52 subpart comparisons have intervals that include zero, while the Week 96 Total Score comparisons also have intervals spanning zero. This is broadly consistent with the primary Week 52 result, which does not show a precise dose-versus-placebo difference. The delayed-start and early-start context at Week 96 differs from the original placebo-controlled comparison, so those findings should not be treated as a direct repeat of the primary contrast.

Secondary outcomes are generally less decisive than the primary endpoint for answering the study's central question. The registry record does not report whether the secondary analyses were adjusted for multiple comparisons, nor does it report a hierarchical testing plan. When many outcomes, time points, or dose comparisons are examined, some apparently notable results may arise by chance. Unless an analysis plan controls that multiplicity, secondary findings are best treated as descriptive or exploratory and interpreted with their uncertainty rather than as stand-alone confirmatory evidence.

The secondary outcomes broaden the view of what was measured, but they do not remove the uncertainty in the primary comparison. A pattern of results across clinical scores may provide context, while safety and pharmacokinetic measures answer different questions. The record does not report enough detail to rank all secondary findings by prespecified importance or to determine how the analysis plan handled the full set of outcomes.

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

• Percentage of Participants With Adverse Events (AEs) and Serious Adverse Events (SAEs)
• Change From Baseline in MDS-UPDRS Total Score (Sum of Parts I, II, and III) at Week 96
• Serum Concentration of BIIB054
• Change From Baseline in MDS-UPDRS Subpart I Score at Week 52
• Change From Baseline in MDS-UPDRS Subpart I Score at Weeks 72 and 96
• Change From Baseline in MDS-UPDRS Subpart II Score at Week 52
• Change From Baseline in MDS-UPDRS Subpart II Score at Weeks 72 and 96
• Change From Baseline in MDS-UPDRS Subpart III Score at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score and is summarized using means. For a continuous outcome, a mean describes the central average across participants, while a mean difference compares average outcomes between groups. The reported primary arm means are adjusted mean changes from baseline. The estimated differences are presented as BIIB054 group minus placebo, so a negative value indicates a lower mean change in the BIIB054 group and a positive value indicates a higher mean change. Because higher MDS-UPDRS scores indicate more severe symptoms, direction needs to be interpreted alongside the outcome definition and the fact that these are changes from baseline.

What does the repeated-measures model do?

The registry reports a Mixed Model for Repeated Measures analysis. In general, this type of model analyzes measurements collected over time while accounting for their correlation within a participant. Rather than treating every visit as an unrelated observation, it uses the repeated structure to estimate group differences over time. It can also use available repeated observations from participants who do not have a complete set of visits, subject to the model and its assumptions. The registry record does not report the detailed model specification, covariance structure, covariates, or missing-data assumptions, so those aspects cannot be assessed from the posted description.

The Week 52 sponsor estimates are -0.30, 0.50, and 0.08, with 95% confidence intervals and p-values reported for each dose-versus-placebo comparison. These are the model-based inferential results. A confidence interval expresses uncertainty around an estimate under the analysis assumptions. If an interval includes zero, the data are compatible with no difference as well as with some differences in either direction. It is not a statement that all values inside the interval are equally likely, nor does it provide a probability that the true effect lies in the interval.

How do the recalculations differ?

The separate recalculations use the posted arm means, standard errors, and analyzed sample sizes to form simple, unadjusted comparisons. They are not a recreation of the repeated-measures model. The recalculated intervals and p-values are consequently not identical to the sponsor's model-based results. They serve as a transparent check on the scale and broad direction of the posted comparison, not as a replacement for the sponsor's analysis. The registry record does not identify a discrepancy between the sponsor analysis and the recalculations.

Standard errors describe the estimated uncertainty of a mean, rather than the spread of individual participant scores. The primary arm summaries report standard errors. In general, a standard error tends to be smaller when an estimate is based on more information and larger when the observed data are more variable. A standard error is not interchangeable with a standard deviation: the former concerns precision of an estimate, while the latter describes variation among observations.

What do the p-values say?

A p-value evaluates how compatible the observed data are with a specified null model, assuming the model and analysis conditions hold. A large p-value does not prove that the groups are identical or that an effect is absent. A small p-value would also not, on its own, communicate the size or clinical importance of a difference. Here, all three sponsor-reported p-values are large, and all three intervals include zero. The result is therefore best described through the estimated differences and their uncertainty, rather than a binary significant-or-not label.

In general, confidence intervals can be more informative than p-values because they display both an estimate and a range of values compatible with the analysis. Precision depends on factors such as sample size, variability, and the analysis design. The unequal analyzed group sizes, especially the smaller 250 mg group, contribute to the context for interpreting precision, but the reported intervals already reflect the sponsor model's estimated uncertainty.

Why does over-dispersion matter?

Over-dispersion is a general issue for outcomes where observed variability exceeds what a statistical model expects. It can make standard errors too small if a model fails to account for that extra variation, leading to confidence intervals that are too narrow and p-values that appear more persuasive than warranted. The primary outcome is a continuous score, and the registry record does not report an over-dispersion assessment. The concern is therefore a general statistical concept, not a reported feature of this analysis.

Finally, the arm summaries and model comparisons answer related but different descriptive questions. Arm means show the average change in each group; the model estimate addresses the randomized comparison using repeated measurements. Neither alone resolves uncertainty about unreported design decisions, missing-data mechanisms, or the clinical importance threshold for the score. The registry record does not report a threshold for a clinically important difference.

11. Confidence Intervals and Precision

The sponsor's Week 52 95% confidence intervals are -4.888 to 4.287 for 250 mg versus placebo, -3.310 to 4.312 for 1250 mg versus placebo, and -3.805 to 3.956 for 3500 mg versus placebo. Each contains zero, so the posted results do not rule out no average difference. Each also spans values on both sides of zero, leaving uncertainty about the direction and size of the group difference.

In general, a confidence interval is a range of estimates compatible with the observed data under the analysis model and its assumptions. A 95% confidence interval is not a guarantee that the particular interval contains the true effect, and its endpoints should not be treated as hard boundaries on all plausible effects. A wide interval signals limited precision relative to the scale of possible differences; a narrower interval would indicate greater precision. The registry record does not report a threshold that would define which score differences are clinically important, so statistical uncertainty cannot be translated into a judgment about clinical importance from these data alone.

The analyzed group counts were 53 for placebo, 29 for 250 mg, 57 for 1250 mg, and 51 for 3500 mg. The 250 mg comparison has the smallest BIIB054 analyzed group and its interval is broad. Differences in analyzed counts and the repeated-measures model both form part of the precision context. The sponsor's intervals are the relevant ones for the reported model; the simple recalculated intervals use a different, unadjusted approach.

All three sponsor intervals overlap substantially and include zero. This does not demonstrate that the dose groups are equivalent; an equivalence conclusion would require an appropriate design and prespecified margin, neither of which is reported in the registry record. The intervals instead show that the Week 52 comparisons remain uncertain across a range of possible differences.

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 displays are planning illustrations based on the observed effect, not the original trial design. For these continuous outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning row uses the stated fraction of the observed effect as the effect to detect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions if that effect were the true one. The 90% power column gives the corresponding number for a higher chance of detection. These are planning quantities, not guarantees about the outcome of a future study. They depend on the assumptions used, including the effect size chosen and the variability estimate.

The rows for 100%, 75%, and 50% of the observed effect illustrate how planning requirements change when the assumed target effect is smaller. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. The displays are not a reconstruction of the trial's intended enrollment or allocation, and the study's actual enrolled sample is not evidence that it had a particular probability of detecting an effect. This is 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 = -0.300; pooled standard deviation σ = 10.729.
2. n = 2 × (1.96 + 0.842)² × 10.729² / -0.300² = 20,078.7, rounded up to 20,079 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 <- -0.299999999999999                      # observed difference in means
sigma <- 10.7292784077029                     # 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(3318523)
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 = 20,079 (80% power), 26,880 (90% power)
 75% of observed effect: n per arm = 35,696 (80% power), 47,787 (90% power)
 50% of observed effect: n per arm = 80,315 (80% power), 107,519 (90% power)
power.t.test: 20079.7 
Simulated power at n = 20,079 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry's own primary analysis uses a Mixed Model for Repeated Measures. It reports differences of -0.30 for BIIB054 250 mg versus placebo, 0.50 for 1250 mg versus placebo, and 0.08 for 3500 mg versus placebo. The corresponding 95% confidence intervals are -4.888 to 4.287, -3.310 to 4.312, and -3.805 to 3.956; the p-values are 0.898, 0.796, and 0.970.

The recalculated comparisons use posted summary statistics for a simple unadjusted comparison. They yield estimates of -0.3, 0.51, and 0.08, with intervals of -5.112 to 4.512, -3.559 to 4.579, and -4.089 to 4.249. These results tell a similar broad story: estimates are close to zero and the intervals include zero. Minor differences are unsurprising because the recalculation does not reproduce the repeated-measures model or its adjustments.

The sponsor's model-based analysis is the main inferential result to interpret. The registry record does not identify a discrepancy between that analysis and the simple recalculations. The latter are useful as a check on the order and direction of the comparison, but they should not be mistaken for the prespecified analysis or treated as an independent confirmation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines multiple doses, outcomes, time points, or statistical comparisons. Each additional test creates another opportunity for a result to appear unusual by chance, even when no underlying difference exists. A prespecified testing hierarchy or an adjustment procedure can help control the overall chance of false-positive conclusions. The registry record does not report whether the Week 52 dose comparisons or the secondary outcomes were adjusted for multiplicity, or whether a hierarchical testing strategy was used.

This omission affects how confirmatory the individual p-values can be considered. The primary outcome is clearly identified, but there are three dose-versus-placebo comparisons, and the registry lists numerous secondary measures. Without a reported multiplicity strategy, the p-values should be read as results for their individual model comparisons rather than as a complete family-wise assessment across every endpoint and comparison. The broad pattern and confidence intervals remain important, but isolated secondary findings would carry less weight.

The record defines the primary analysis population as randomized participants who received at least one dose of study treatment. This is the registry's stated definition; it is not a conventional all-randomized intention-to-treat definition because receipt of at least one dose is required. Outcome-specific analyzed numbers are reported, but the registry record does not report detailed reasons for differences between the randomized population and those included in each analysis.

The registry record also does not report the missing-data strategy, the assumptions used for unobserved outcome values, sensitivity analyses for missing data, or how protocol deviations were handled. These details matter because repeated-measures estimates may depend on the pattern and assumptions about missing observations. Nor are interim analyses, stopping rules, or the original sample-size justification reported. The study status is terminated, but the reason for termination is not reported in the registry record. These absences limit assessment of how fully the posted analyses reflect the intended design and how robust the results are to alternative 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: bradycardia (5.0%), transient ischaemic attack (5.0%), anaphylactic reaction (2.7%), covid-19 (2.7%), covid-19 pneumonia (2.7%).

The registry reports serious adverse events by treatment-period group, with a number at risk and a number affected for each group. In the primary-completion period, serious adverse events were recorded for 7 of 100 participants in the placebo group, 4 of 55 in the 250 mg early-start group, 4 of 102 in the 1250 mg early-start group, and 6 of 100 in the 3500 mg early-start group. Delayed-start groups and early-start groups are also listed for the later period, with their own numbers at risk and affected. These are counts from different treatment-period groups and should be read with those group definitions in mind.

The registry lists zero deaths in each group except the DBE Period BIIB054 3500 mg early-start group, where one death is recorded. The record does not establish that this death was caused by BIIB054. Serious-event terms listed among the most frequent include Bradycardia and Transient ischaemic attack at 5.0% each, and Anaphylactic reaction, COVID-19, COVID-19 pneumonia, and Arthropod sting at 2.7% each.

These counts describe reported events; they do not by themselves establish comparative safety or causation. The record does not provide enough information about exposure time, event timing, adjudication, or individual clinical context to interpret the counts as rates or attribute events to treatment. Serious adverse event counts also differ from the separate counts for other adverse events.

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

The Week 52 primary result is an estimate of average change in MDS-UPDRS Total Score for each BIIB054 dose group relative to placebo. The posted estimates are close to zero, and each sponsor-reported 95% confidence interval includes zero. The results do not provide a precise estimate of a dose-versus-placebo difference, and they do not establish a clear dose-related pattern among the three early-start groups.

This does not mean the groups have been shown to be equivalent. A failure to identify a clear difference is not proof that no difference exists, especially when confidence intervals allow values in either direction. Nor do the results establish that any observed within-group change was caused by treatment: changes within each group include influences beyond the randomized comparison. The primary interpretation rests on the between-group estimates and their uncertainty.

The endpoint measures a broad score covering non-motor experiences, motor experiences of daily living, and motor signs. It does not encompass every possible aspect of Parkinson's disease or every outcome that may matter to participants. The registry record does not report a threshold for a clinically important difference, so the clinical meaning of particular score differences cannot be determined from a statistical interval alone.

The study's status is terminated, and the reason is not reported in the registry record. The primary endpoint is reported for a subset of the enrolled population, and details of missing-data handling are not reported. These considerations, together with unreported multiplicity procedures and design assumptions, qualify how far the posted results can be generalized or interpreted as definitive evidence.

The findings are best understood as the estimates and uncertainty recorded for this trial's analyzed groups and time point. They neither prove benefit nor prove lack of benefit. They also do not provide medical advice or a basis for an individual treatment decision.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be interpreted without its confidence interval. The Week 52 differences are numerically near zero, but the intervals extend across zero and cover a range of possible group differences. Looking only at a p-value, or only at the arm means, would omit important information about uncertainty and the randomized comparison.

It also illustrates the distinction between an adjusted longitudinal model and a simple calculation from summary statistics. The sponsor's Mixed Model for Repeated Measures analysis incorporates repeated outcome measurements, while the recalculation is a simpler unadjusted comparison. Their results are similar in broad interpretation but are not identical. Knowing which analysis answers the study's primary question helps avoid treating different statistical methods as interchangeable.

The design has early-start and delayed-start treatment periods, so comparisons at Week 52 and Week 96 have different contexts. Recognizing that distinction is important when considering whether later outcomes reinforce the primary comparison. The secondary results add descriptive context, but unreported multiplicity handling limits their confirmatory interpretation.

Finally, the record highlights reporting details that affect statistical appraisal: the trial was terminated, outcome-specific analyzed counts are smaller than enrollment, and information about the reason for termination, missing-data methods, original sample-size justification, and multiplicity procedures is not reported. Such details are not peripheral. They inform how confidently readers can connect the estimates to the planned question and how much weight to place on secondary patterns.

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 analysis includes fewer participants than the total enrollment, and the numbers analyzed differ across arms. The registry defines the population as randomized participants who received at least one dose, but does not detail why participants were not included in each outcome analysis. Without the missing-data approach and sensitivity analyses, it is not possible to assess how assumptions about unavailable measurements may affect the estimates.

The registry record does not report the reason the study was terminated, original sample-size assumptions, or the planned statistical analysis details beyond the named repeated-measures method. It also does not report a multiplicity strategy for the three dose comparisons and the many secondary measures. These gaps constrain interpretation of how confirmatory the p-values are and whether the posted analysis fully reflects the trial's intended testing framework.

The treatment periods complicate comparisons across time. Placebo participants were assigned active treatment in Year 2, while the early-start groups had already received BIIB054. Therefore, the Week 96 pooled delayed-start group and early-start dose groups are not the same comparison as placebo versus early-start treatment at Week 52.

The primary result is based on adjusted means, but the registry does not describe the adjustment variables, model covariance structure, or detailed assumptions. The simple recalculations are not a substitute for that model. The registry also does not report a clinical-importance threshold for MDS-UPDRS change, limiting interpretation of the magnitude of differences in clinical terms. Safety counts are reported for treatment-period groups, but exposure duration and detailed event context are not included in these figures.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluating the Efficacy, Safety, Pharmacokinetics, and Pharmacodynamics of BIIB054 in Participants With Parkinson's Disease — NCT03318523.
• Registry record last updated 2022-02-28; status last verified 2022-02.
• Results first posted 2021-11-23.
• 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

NCT03318523 is a randomized phase 2 study of BIIB054 in participants with Parkinson's disease. It enrolled 357 participants and compared placebo with three early-start BIIB054 doses during the primary-completion period. The primary endpoint was change from baseline in MDS-UPDRS Total Score at Week 52.

The sponsor's repeated-measures estimates versus placebo were -0.30 for 250 mg, 0.50 for 1250 mg, and 0.08 for 3500 mg. All three reported 95% confidence intervals include zero. The registry also lists secondary outcome and safety results, with treatment-period groupings that include delayed-start participants.

The record reports that the study is terminated. It does not report the reason for termination, detailed missing-data methods, multiplicity procedures, or the original sample-size justification. The posted results should therefore be read as uncertain estimates from the analyzed groups, not as proof of equivalence or a definitive dose-response conclusion.