Safety and Efficacy Study of ELND005 as an Adjunctive Maintenance Treatment in Bipolar I Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of ELND005 as an Adjunctive Maintenance Treatment in Bipolar I Disorder (NCT01674010), a randomized phase 2 study. The primary outcome is Treatment Emergent Adverse Events.

2. Clinical Question

The record identifies recurrence of any mood episode, time to depressive episode recurrence, and time to manic/hypomanic or mixed episode recurrence as secondary outcomes. Those outcomes provide context for the planned maintenance question, but no analyses of efficacy are posted. The record does not report the reason for early termination or further details of the treatment period actually completed by participants. The statistical interpretation must therefore stay with the available safety counts and the unadjusted comparisons posted for those counts.

3. Trial Design

This was a randomized, quadruple-masked, parallel Phase 2 study sponsored by OPKO Health, Inc. The registry lists enrollment of 309 and describes the study as a prospective, randomized, double-blind, placebo-controlled investigation of oral ELND005 as adjunctive maintenance treatment for bipolar I disorder. The treatment plan paired ELND005 or matched placebo with lamotrigine or valproic acid for up to 48 weeks.

The Phase 2 safety groups comprise 65 participants in the placebo group and 64 in the ELND005 500 mg BID group. The registry also reports an open treatment Phase 1 group of 309 participants receiving ELND005 500 mg BID. That group is presented separately from the masked Phase 2 comparison. Its outcome count should not be read as a randomized comparison against the Phase 2 placebo group: the registry labels it open treatment and does not report an analysis establishing comparability between these groups.

The study status is terminated. The primary outcome timeframe is described as up to 48 weeks, while the primary outcome description says the study was terminated early, so no efficacy analysis was done and safety data are reported. The record gives start and primary completion dates, but does not describe the circumstances or timing of termination in enough detail to explain exposure or follow-up for each participant.

Details such as the randomization method, allocation concealment, planned sample-size justification, and the original statistical analysis plan are not reported in the registry record. The listing of masking as quadruple does not identify the roles of all masked parties. These limits matter when judging how fully the posted safety counts represent the planned trial design.

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.

Open Treatment Phase 1

Reasons for not completing this period:

Randomization Phase 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: TEAEs reported for Phase 2 were from the entire study period

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 Treatment Emergent Adverse Events, measured over up to 48 weeks.

The posted primary outcome is Treatment Emergent Adverse Events (TEAEs), reported as the number of participants with an event. A TEAE is an adverse event that emerges during the treatment period; the registry describes the Phase 2 TEAE data as covering the entire study period. This endpoint is used in safety reporting because it counts participants who experienced an adverse event during exposure, rather than measuring a change in a clinical symptom or a time-to-event efficacy outcome.

The Phase 2 figures are 45 participants with TEAEs among 65 in the placebo group and 45 among 64 in the ELND005 group. The separate open treatment Phase 1 group reports 153 among 309. These counts describe how many participants were reported with events in each registry group; they do not describe the number, duration, or severity of all events experienced by each participant. The record does not provide event-specific detail for the full TEAE outcome in these primary results.

The endpoint is relevant to safety monitoring, but it cannot answer the planned efficacy question about maintenance treatment. The registry explicitly states that no efficacy analysis was done. Nor does a count of participants with any TEAE, by itself, distinguish mild events from serious events, establish causation, or show the clinical importance of individual events. Serious adverse events are reported separately and should be interpreted as a distinct safety measure.

7. Results Posted in the Registry

• Open Treatment Phase 1 ELND005 500 mg BID: 49.5% (153/309) versus 69.2% (45/65) on control; risk difference -19.7 percentage points (95% CI -32.2 to -7.2), risk ratio 0.72 (0.59–0.87); unadjusted two-proportion z-test p = 0.004.
• Phase 2 ELND005 500 mg BID: 70.3% (45/64) versus 69.2% (45/65) on control; risk difference 1.1 percentage points (95% CI -14.8 to 16.9), risk ratio 1.02 (0.81–1.27); unadjusted two-proportion z-test p = 0.894.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a binary participant-level measure: each participant is counted according to whether a TEAE was reported. For a binary outcome, the risk is the proportion of participants in a group who had the event. A risk difference expresses the difference between those group risks. General interpretation: a risk difference near zero indicates similar observed proportions, while its sign indicates which group has the larger observed proportion under the stated comparison order. This summary does not convey event frequency per participant or event severity.

For the Phase 2 comparison, the posted unadjusted risk difference is 0.011. The interval runs from -0.148 to 0.169, and the unadjusted p-value is 0.894. The estimate and interval are the appropriate starting points: the estimate describes the observed contrast, and the interval describes uncertainty around that estimate under the calculation's assumptions. The p-value is not the probability that the null hypothesis is true, nor does it indicate the probability that treatment caused an event. It measures how compatible the observed data are with a specified no-difference model, under the assumptions of the test.

General explanation: a confidence interval represents a range of values that are reasonably compatible with the data and the statistical model at the stated confidence level. A wide interval signals limited precision; an interval crossing zero for a risk difference means the data are compatible with no difference as well as differences in either direction. The registry does not state the confidence level or the exact calculation method for these comparisons, so those details are not reported in the registry record. The p-values are explicitly unadjusted; the record does not describe an adjustment for multiple comparisons.

The open treatment Phase 1 comparison has an unadjusted risk difference of -0.197, with an interval from -0.322 to -0.072 and an unadjusted p-value of 0.004. The arithmetic describes a contrast between the posted groups, but statistical significance does not resolve whether that contrast is attributable to treatment. The groups belong to different phases, and the Phase 1 group is labelled open treatment. A test of a difference cannot correct for differences in study context or participant composition that the record does not describe. It should not be treated as the randomized Phase 2 estimate.

Risk ratios and odds ratios are also listed for both comparisons. General explanation: a risk ratio compares event risks, while an odds ratio compares event odds; each uses a different scale from a risk difference. These measures can complement a risk difference, but they do not overcome limitations in design or missing analysis details. The main interpretation should remain anchored to the Phase 2 group counts, the risk difference, and its interval.

Serious adverse events are reported as participant counts by group. The counts are 3 in Phase 2 placebo, 3 in Phase 2 ELND005, and 12 in open treatment Phase 1. The record supplies no confidence intervals or inferential comparisons for these figures. They should therefore be treated as descriptive safety information rather than evidence of a tested group difference. Serious event terms and listed percentages are also descriptive; the registry does not supply the denominators or analysis details needed to make a comparative claim about individual terms.

The registry's sample-size illustrations use the observed effect as a planning reference, with the effect to detect set to a stated fraction of that observed effect. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial's design assumptions are not reported in the registry record. The planning estimates are not evidence about the trial's achieved power and should not be confused with observed results.

For binary outcomes, general explanation: over-dispersion means observed variability exceeds what a simple model assumes. If present, it can make standard errors too small and confidence intervals too narrow unless the analysis accounts for it. The registry does not report whether over-dispersion was assessed or whether a model beyond the unadjusted comparisons was used. The posted information also does not describe covariate adjustment, stratification, the handling of repeated events, or the statistical approach for time-to-recurrence outcomes. Those methods are not reported in the registry record.

10. Confidence Intervals and Precision

The Phase 2 TEAE risk difference is 0.011, with a confidence interval from -0.148 to 0.169. This interval crosses zero, so the posted data are compatible with no difference in the observed TEAE proportions as well as with differences in either direction. The interval is broad relative to the point estimate, indicating that the comparison is not precise enough to pin down a narrow range of plausible differences. The counts themselves are close, but similar observed counts do not guarantee that the underlying risks are identical.

General explanation: confidence intervals help show how much uncertainty remains around an estimate. A point estimate is the central result of the calculation; it is not the only plausible value supported by the data. The lower and upper limits describe uncertainty under the statistical method and its assumptions. The registry does not report the confidence level or calculation method for these comparisons, so those details are not reported in the registry record.

The open treatment Phase 1 comparison has a risk difference of -0.197 and an interval from -0.322 to -0.072. Although that interval does not cross zero, its statistical precision does not make this a randomized comparison. It contrasts an open Phase 1 group with Phase 2 placebo, and the record does not establish that the groups can be compared as if randomized. Precision about a contrast is not the same as confidence that the contrast is causal.

No confidence intervals are posted for the serious adverse event counts. The registry also does not provide inferential results for the secondary efficacy outcomes. Accordingly, the precision of those safety counts and any potential treatment effects on mood-episode recurrence cannot be assessed from the posted results.

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 sample-size planning illustrations are based on the observed effect and are not the original trial's design justification. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is the stated fraction of the observed effect. The original design assumptions are not reported in the registry record.

For the Phase 2 ELND005 comparison, planning for 100% of the observed effect gives 28,293 participants per arm for 80% power and 37,876 participants per arm for 90% power. Planning for 75% of the observed effect gives 50,427 participants per arm for 80% power and 67,506 participants per arm for 90% power. Planning for 50% of the observed effect gives 113,745 participants per arm for 80% power and 152,271 participants per arm for 90% power. These large illustrations reflect the small observed risk difference in this comparison; they are not enrollment targets from the trial record.

For the open treatment Phase 1 versus placebo comparison, the corresponding estimates are 97 and 129 participants per arm for 100% of the observed effect, 169 and 225 for 75%, and 370 and 495 for 50%, for 80% and 90% power respectively. Because this comparison crosses study phases and includes an open treatment group, these figures should not be used as a design recommendation for a randomized trial without considering that limitation.

In general, the 80% power column indicates the planning number per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions; the 90% column indicates the number for a 90% chance. Smaller effects require more participants under the same assumptions. These are planning illustrations, not observed power. The record's assumptions specify participants per arm for these binary-outcome comparisons; time-to-event calculations, if present, are expressed as total events rather than participants per arm.

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 = 0.692; treatment proportion p₁ = 0.495; average p̄ = 0.594.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6946 = 1.3613.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6804 = 0.5727.
4. n = (1.3613 + 0.5727)² / (-0.1972)² = 96.2, rounded up to 97 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 <- 0.692307692307692                          # control proportion
p1 <- 0.495145631067961                          # 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(1674010)
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 = 97 (80% power), 129 (90% power)
 75% of observed effect: n per arm = 169 (80% power), 225 (90% power)
 50% of observed effect: n per arm = 370 (80% power), 495 (90% power)
power.prop.test: 96.2 
Simulated power at n = 97 per arm: 0.799 (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 three secondary outcomes: the proportion of participants with recurrence of any mood episode, time to recurrence of a depressive episode, and time to recurrence of a manic/hypomanic or mixed episode. These outcomes relate to the intended maintenance question, but no efficacy analysis was done, and no analyses are posted for them. The registry does not report an analysis hierarchy, a family-wise error strategy, or another method for controlling multiplicity. Those details are not reported in the registry record.

The record identifies unadjusted p-values for the posted comparisons. It does not describe whether those comparisons were planned, exploratory, or selected after examining the data. No multiplicity adjustment is reported. When multiple outcomes or comparisons are considered, unadjusted p-values do not account for the greater chance of observing a nominally unusual result across the full set of tests. This is especially relevant to the open Phase 1 comparison, which should not be read as the randomized Phase 2 treatment contrast regardless of its p-value.

Missing-data procedures are not reported in the registry record. The record does not state how participants with incomplete treatment exposure, missing outcome information, withdrawal, or loss to follow-up were handled. It also does not specify an intention-to-treat, per-protocol, or safety analysis population definition for the posted comparisons. Although safety group denominators are given, that alone does not establish the analysis population rules or explain whether every participant had the same opportunity for event reporting.

The study was terminated early and the registry says no efficacy analysis was done. The reason for termination, the handling of any incomplete follow-up, and whether any interim analyses occurred are not reported in the registry record. The analysis plan and any prespecified stopping rules are also not reported. Without those details, it is not possible to judge how early termination affected the planned efficacy assessment or whether the posted safety comparisons reflect a complete planned analysis.

These gaps do not invalidate the descriptive counts, but they limit interpretation of inferential results and prevent a full assessment of the planned statistical strategy. The registry record supports a description of the reported safety outcomes; it does not provide enough detail to reconstruct the analysis populations, missing-data handling, or multiplicity approach.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: food poisoning (1.6%), mania (1.6%), diplopia (1.6%), hemolytic anemia (1.5%), pneumonia (1.5%).

The serious adverse event counts are 12 among 309 participants in the open treatment Phase 1 group, 3 among 65 in the Phase 2 placebo group, and 3 among 64 in the Phase 2 ELND005 group. These are counts of participants reported with serious adverse events, as represented in the registry's safety data. They are distinct from the primary TEAE counts, which include participants with treatment-emergent adverse events more broadly.

The Phase 2 serious-event counts are close, but the record does not provide confidence intervals or a statistical comparison for them. The open treatment group is from a different phase and should not be directly compared with the Phase 2 groups as though randomized. The registry lists Food Poisoning, Mania, Diplopia, Hemolytic anemia, Pneumonia, and Abortion spontaneous among the top serious event terms, with percentages shown for those terms. The corresponding denominators and further event-level context are not reported in the registry record.

Deaths are not reported in the posted group data. Serious-event counts and term listings are descriptive and do not establish that an event was caused by treatment.

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

The posted Phase 2 safety results show the same count of participants with TEAEs in the placebo and ELND005 groups: 45 in each group. Their denominators differ, and the unadjusted risk-difference estimate is 0.011 with a confidence interval from -0.148 to 0.169. This is a description of the registry's observed safety data. The interval indicates uncertainty that includes no difference and possible differences in either direction; it does not demonstrate equivalence or prove that the groups have the same underlying risk.

The record also reports serious adverse events for 3 participants in each Phase 2 group. These counts have no accompanying inferential comparison in the registry. They are not enough to establish that serious-event risks are equal, and they do not describe the full range of event types, timing, or severity. The separate open treatment Phase 1 safety group has higher posted counts, but a comparison with Phase 2 placebo is not a randomized treatment-effect estimate.

Most importantly, the registry states that early termination meant no efficacy analysis was done. The listed secondary outcomes concern recurrence of mood episodes and time to recurrence, but there are no posted efficacy estimates for them. The available results therefore do not answer whether ELND005 changed the maintenance course of bipolar I disorder.

These findings also do not establish that ELND005 is safe or unsafe in general. The posted data cover the study groups and reporting described in the registry, while details about follow-up, missing information, event-level context, and the analysis populations are limited. The results should be read as the safety counts and unadjusted comparisons recorded, not as a complete assessment of treatment benefit or risk.

16. Why This Trial Matters Statistically

This trial illustrates why the statistical question and the available result need to be kept distinct. The stated purpose concerned adjunctive maintenance treatment, but the posted primary outcome is a safety measure, and the registry says no efficacy analysis was done after early termination. A reader cannot substitute safety counts for the planned question about mood-episode recurrence.

It also shows the importance of separating a randomized comparison from a contrast across different study phases. The Phase 2 placebo and ELND005 groups are the relevant masked comparison described in the trial design. The open treatment Phase 1 group has its own safety counts, but its comparison with Phase 2 placebo does not have the same design basis. A small p-value for that contrast does not remove concerns about comparability.

The Phase 2 risk difference is close to zero, yet its interval extends across values in both directions. This demonstrates why a point estimate alone is not enough: uncertainty must be considered, and a non-significant p-value does not prove no effect. Similarly, the planning illustrations based on the observed effect are highly dependent on the size of that estimate and the stated assumptions. They do not explain the original design or establish what the completed trial could detect.

Finally, incomplete reporting of analysis populations, missing-data handling, multiplicity, and termination details limits reconstruction of the statistical plan. Clear distinctions between descriptive counts, unadjusted comparisons, and prespecified efficacy analyses are essential to avoid overstating what the registry record can support.

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.

The most important limitation is that the study was terminated and no efficacy analysis was done. Although the record lists recurrence-related secondary outcomes, it provides no efficacy estimates for them. The reason for termination and its implications for follow-up are not reported in the registry record, so the completeness of outcome observation cannot be assessed.

The posted Phase 2 TEAE comparison has an interval that includes zero and extends across a range of possible risk differences. The result is therefore imprecise and should not be interpreted as evidence of equivalence. The registry does not report the confidence-interval method, confidence level, or a fuller statistical analysis plan. It also does not describe missing-data handling, analysis populations, or any covariate adjustment.

The open treatment Phase 1 group is not the randomized Phase 2 comparator. Its comparison with Phase 2 placebo combines groups from different phases, and the record does not establish their comparability. Any difference between those groups could relate to study phase, participant composition, exposure, or other unreported factors, rather than treatment alone.

Serious adverse event results are reported as counts without confidence intervals or formal comparisons. Death counts are not reported in the registry record. For the listed serious event terms, denominators and additional event-level details are not reported in the registry record. The registry also does not state how many participants completed the planned treatment period or how long each participant was followed. These limitations constrain interpretation of the safety profile as well as any comparison of groups.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of ELND005 as an Adjunctive Maintenance Treatment in Bipolar I Disorder — NCT01674010.
• Registry record last updated 2019-10-21; status last verified 2019-10.
• Results first posted 2015-10-12.
• 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

NCT01674010 is a randomized, quadruple-masked, parallel Phase 2 study of oral ELND005 as adjunctive maintenance treatment for bipolar I disorder. The planned treatment was ELND005 500 mg BID or matched placebo, added to lamotrigine or valproic acid, for up to 48 weeks. The registry reports an enrollment of 309 and a terminated study status.

The posted primary outcome is Treatment Emergent Adverse Events, measured as participants with events. Phase 2 counts are 45 of 65 for placebo and 45 of 64 for ELND005. The record states that the study was terminated early and no efficacy analysis was done. Serious adverse event counts are reported separately. The registry does not report the reason for termination, detailed missing-data methods, analysis-population definitions, or the original sample-size assumptions.