Ventilatory Investigation of Tirasemtiv and Assessment of Longitudinal Indices After Treatment for a Year: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ventilatory Investigation of Tirasemtiv and Assessment of Longitudinal Indices After Treatment for a Year (NCT02496767), a randomized phase 3 study. The primary outcome is Change From Baseline to Week 24 of the Double-blind, Placebo-controlled Phase in Percent Predicted Slow Vital Capacity (SVC).

2. Clinical Question

The registry record identifies the study as a phase 3 evaluation of tirasemtiv safety, tolerability and efficacy in ALS. Its primary endpoint focuses on respiratory function rather than a broad measure of overall disease status. The randomized, masked, parallel-group comparison is intended to evaluate differences in the endpoint between treatment assignment groups, with placebo serving as the control.

The endpoint is a change score: it concerns movement from each participant’s baseline value through Week 24, not the absolute SVC measurement at Week 24 alone. The primary results are reported as least-squares means with standard errors, and the sponsor’s comparison is reported as a least-squares mean difference from placebo. The statistical question is therefore whether the observed between-group estimates are compatible with no difference, and how much uncertainty surrounds those estimates. A comparison cannot establish a clinically important effect solely from its direction; interpretation also depends on the estimate’s precision, the endpoint’s clinical context and the study’s analysis plan.

3. Trial Design

The registry record describes a phase 3, multi-national, double-blind, randomized, placebo-controlled, stratified, parallel-group study. It lists an enrollment of 744 and a completed status. The study started on 2015-09-03, and primary completion was recorded as 2017-03-09. The sponsor was Cytokinetics.

The study compared placebo with three tirasemtiv dose groups: 250 mg, 375 mg and 500 mg. The primary assessment was change in percent predicted SVC from baseline to Week 24 of the double-blind, placebo-controlled phase. The record also lists treatment and secondary assessments extending to 48 weeks. The placebo group and tirasemtiv groups have separate reported analysis sample sizes for the primary endpoint: 188.0, 126.0, 125.0 and 122.0, respectively. These are analysis-set counts, not a restatement of total enrollment.

The registry describes an open-label lead-in and double-blind withdrawal groups in its adverse-event information, in addition to the principal double-blind treatment groups. The full sequence of these study periods, eligibility or transition rules, and the number of participants moving between periods are not reported in the registry record. The available dose descriptions identify some daily tablet schedules, but they do not provide complete schedules for every group and period.

Triple masking is listed, but the masked roles are not reported in the registry record. The stratification factors are not reported in the registry record. The registry also does not report the original sample-size justification or a detailed protocol for handling treatment adherence, rescue interventions or discontinuation. Those omissions limit how fully the design can be reconstructed from the registry entry alone.

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: All enrolled patients began open-label tirasemtiv (250 mg) in a 2-week lead-in phase. Completed patients were randomized (3:2:2:2) to placebo or tirasemtiv (250, 375, or 500 mg) for 48 weeks of double-blind treatment. After which, patients on tirasemtiv were re-randomized (1:1) to placebo or tirasemtiv (current dose) for a 4-week withdrawal phase.

Only the first 6 of 8 groups are shown.

Open-label Lead-in Phase

Reasons for not completing this period:

Double-blind, Placebo-controlled Phase

Reasons for not completing this period:

Double-blind, Withdrawal Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The data presented are for the Full Analysis Set, comprised of patients who received at least 1 dose of study drug during the randomized double-blind, placebo-controlled phase and had at least 1 post-randomization efficacy assessment.

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: Baseline Characteristics are provided for the Full Analysis Set, comprised of patients who received at least 1 dose of study drug during the randomized double-blind, placebo-controlled phase and had at least 1 post-randomization efficacy assessment (totaling 561 patients: 188, 126, 125, and 122 patients in Groups 1, 2, 3, and 4, respectively).

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Week 24 of the Double-blind, Placebo-controlled Phase in Percent Predicted Slow Vital Capacity (SVC), measured over 24 weeks.

The primary endpoint is change from baseline to Week 24 in percent predicted slow vital capacity (SVC). SVC is a spirometric measure of the volume of air a person can exhale after taking as deep a breath as possible. The registry describes a procedure involving breaths at rest, a maximal inspiration and a maximum exhalation. Measurements in liters were converted to percent predicted values, using predicted values for people with similar demographic and baseline characteristics, based on Knudson 83 normative values.

Expressing SVC as percent predicted places the measured lung volume in the context of expected values for characteristics such as height, age and sex. The endpoint is therefore not simply the raw volume in liters. A change from baseline describes how that relative respiratory measure shifted over the assessment period. The registry reports least-squares mean change and standard error for each group, along with sponsor-reported between-group least-squares mean differences and confidence intervals.

SVC is used in this study as an objective respiratory-function measure. It complements symptom and functional measures, but it captures a specific aspect of respiratory capacity rather than the full experience or course of ALS. The registry record does not report a threshold for what change would be clinically important, so statistical estimates should not be treated as establishing clinical importance on their own.

7. Results Posted in the Registry

• Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv: mean -12.65 versus -14.35 on control; difference 1.71 (95% CI -2.12 to 5.53), standardized effect d = 0.10; z-test p = 0.382.
• Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv: mean -13.74 versus -14.35 on control; difference 0.61 (95% CI -3.35 to 4.58), standardized effect d = 0.04; z-test p = 0.762.
• Double-blind, Placebo-controlled: Group 4 - 500 mg Tirasemtiv: mean -13.93 versus -14.35 on control; difference 0.43 (95% CI -3.72 to 4.57), standardized effect d = 0.02; z-test p = 0.840.

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 the ALSFRS-R Respiratory Domain Score at the End of 48 Weeks of Double-blind, Placebo-controlled Treatment

• 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:
  • Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv: mean -1.95 versus -2.26 on control; difference 0.31 (95% CI -0.50 to 1.12), standardized effect d = 0.09; z-test p = 0.451.
  • Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv: mean -2.41 versus -2.26 on control; difference -0.15 (95% CI -0.99 to 0.69), standardized effect d = -0.04; z-test p = 0.725.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv 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 Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv and the control. The interval gives the range of effects that remain compatible with the data.

Time to the First Occurrence of a Decline From Baseline in Percent Predicted SVC ≥ 20 Percentage Points or the Onset of Respiratory Insufficiency or Death All 48 Weeks of Double-blind, Placebo-controlled Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv: 46.0% (58/126) versus 52.1% (98/188) on control; risk difference -6.1 percentage points (95% CI -17.4 to 5.2), risk ratio 0.88 (0.70–1.12); unadjusted two-proportion z-test p = 0.290.
  • Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv: 46.4% (58/125) versus 52.1% (98/188) on control; risk difference -5.7 percentage points (95% CI -17.0 to 5.6), risk ratio 0.89 (0.71–1.12); unadjusted two-proportion z-test p = 0.321.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv 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 Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv and the control. The interval gives the range of effects that remain compatible with the data.

Time to the First Occurrence of a Decline in SVC to ≤ 50% Predicted, or the Onset of Respiratory Insufficiency, or Death During the 48 Weeks of Double-blind, Placebo-controlled Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv: 31.0% (39/126) versus 30.3% (57/188) on control; risk difference 0.6 percentage points (95% CI -9.8 to 11.0), risk ratio 1.02 (0.73–1.43); unadjusted two-proportion z-test p = 0.905.
  • Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv: 24.0% (30/125) versus 30.3% (57/188) on control; risk difference -6.3 percentage points (95% CI -16.3 to 3.6), risk ratio 0.79 (0.54–1.16); unadjusted two-proportion z-test p = 0.222.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind, Placebo-controlled: Group 2 - 250 mg Tirasemtiv 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 Double-blind, Placebo-controlled: Group 3 - 375 mg Tirasemtiv and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary findings cover several aspects of ALS, including respiratory-domain function, muscle strength, SVC-related events, total ALSFRS-R score and use of mechanical ventilatory assistance or death. The available numerical results are incomplete across this list: some secondary outcomes and comparisons are not reported in the registry record. The posted results therefore do not provide a single, comprehensive picture of every prespecified secondary question.

For the outcomes with results, the estimates do not form a consistent pattern of clear separation from placebo. The respiratory-domain score comparisons have confidence intervals spanning no difference. The Cox analyses for the reported SVC-related time-to-event outcomes also have confidence intervals that include the null hazard ratio. The event counts and continuous estimates are useful context, but they do not establish a secondary treatment effect on their own.

These outcomes relate to the primary finding by examining other dimensions or later time points of respiratory and functional status. They are not substitutes for the Week 24 primary SVC endpoint: their definitions, follow-up periods and statistical methods differ. Similarity or difference across outcomes may reflect those distinct measurement choices as well as uncertainty.

Secondary results generally carry less inferential weight when many outcomes and comparisons are tested without a reported multiplicity procedure. A nominal p-value can appear small by chance when many hypotheses are examined. The registry record lists multiple outcomes and analyses, but does not report whether secondary testing was adjusted or hierarchically ordered. Accordingly, isolated secondary findings should be treated as exploratory unless a prespecified testing strategy is available. They should be considered alongside effect estimates, confidence intervals, missing results and the primary analysis rather than used to make a standalone efficacy claim.

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

• Change From Baseline in the ALSFRS-R Respiratory Domain Score at the End of 48 Weeks of Double-blind, Placebo-controlled Treatment
• Slope of Mega-score of Muscle Strength During the 48 Weeks of Double-blind, Placebo-controlled Treatment
• Time to the First Occurrence of a Decline From Baseline in Percent Predicted SVC ≥ 20 Percentage Points or the Onset of Respiratory Insufficiency or Death All 48 Weeks of Double-blind, Placebo-controlled Treatment
• Time to the First Occurrence of a Decline in SVC to ≤ 50% Predicted, or the Onset of Respiratory Insufficiency, or Death During the 48 Weeks of Double-blind, Placebo-controlled Treatment
• Change From Baseline in the ALSFRS-R Total Score to the End of 48 Weeks of the Double-blind, Placebo-controlled Treatment
• Time to the First Use of Mechanical Ventilatory Assistance or Death During All 48 Weeks of Double-blind, Placebo-controlled Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary estimate represent?

The primary outcome is continuous, meaning it is measured on a numerical scale rather than recorded only as an event or category. The registry reports least-squares means for change from baseline and standard errors. A least-squares mean is a model-based group estimate; it is not necessarily the simple arithmetic average of the observed measurements. The model can account for the structure specified by the analysis, but the registry record does not provide all of that specification.

The comparisons are differences between a tirasemtiv group and placebo. A positive estimated difference means the modeled change was less negative, or more positive, in the tirasemtiv group than in placebo. It does not by itself establish a meaningful benefit. The confidence interval indicates the range of estimates compatible with the reported model and data under its assumptions.

Why use a repeated-measures mixed model?

The sponsor reports a repeated-measures mixed model for the primary endpoint. In general, repeated-measures methods analyze observations collected from the same participants at multiple visits. A mixed model can account for the correlation among measurements from one participant, rather than treating every visit as independent. It can also use available repeated observations under model assumptions, though the registry record does not report the missing-data assumptions, covariance structure, adjustment variables or full visit schedule used in this analysis.

This matters because measurements from one person tend to be related over time. Treating correlated observations as independent can misstate uncertainty. A mixed model is one way to represent that dependence, but its estimates still rely on choices about the model and on assumptions about the data. The registry record names the method but does not give enough detail to assess all those choices.

What do the p-values test?

The sponsor’s reported comparisons are labeled as superiority analyses. In general, a superiority test evaluates whether the data support a difference favoring one group over the other under a specified null hypothesis. A p-value describes how unusual the observed data, or more extreme data, would be under that null and the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

For the primary comparisons, the sponsor reports p-values of 0.378, 0.762 and 0.839. These values, considered alongside confidence intervals spanning zero, do not provide evidence of a statistically clear difference from placebo. They do not prove equivalence or show that a clinically relevant effect is impossible. An equivalence or non-inferiority conclusion would require a prespecified margin and an analysis designed for that purpose; such information is not reported in the registry record.

How do the recalculations differ?

The recalculated continuous-outcome comparisons use posted group estimates and standard errors to construct simple unadjusted comparisons. The pooled standard deviations are approximated from the standard errors and group sizes, as indicated in the recalculation details. This approach is useful as a rough cross-check, but it does not reproduce a repeated-measures mixed model. It does not account for covariates, correlations across visits, missing-data handling or other features that may have entered the sponsor analysis.

For that reason, the sponsor’s model-based result is the principal inferential result. The recalculation is supplementary and should not be interpreted as a second independent trial result. The recalculated comparisons are close to the reported model estimates, but small differences between methods are expected when the calculations rely on different information and assumptions.

How are secondary outcomes analyzed?

The secondary outcomes include continuous measures, participant counts and time-to-event outcomes. The registry reports Cox regression hazard ratios for the two posted time-to-event comparisons. In general, a Cox model compares event rates over follow-up while accounting for the timing of events and censoring, under model assumptions. A hazard ratio is not the same quantity as a risk difference or a simple ratio of event counts. The registry record does not report the full Cox model specification or its assumptions.

The posted event counts are informative descriptions, but the time-to-event analysis uses follow-up timing as well as whether an event occurred. A count comparison cannot recreate the Cox model. For continuous secondary outcomes, the sponsor reports repeated-measures mixed models for the respiratory-domain score. Results are not reported in the registry record for every listed secondary outcome and dose comparison.

The registry lists 21 analyses and 7 outcome measures. Multiple outcomes, groups and analyses create opportunities for chance findings. Whether and how the trial controlled the family-wise error rate or adjusted secondary tests for multiplicity is not reported in the registry record. This missing analysis-plan detail affects the weight given to isolated secondary p-values.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a group difference. The primary sponsor-reported 95% confidence intervals are wide enough to include zero for each tirasemtiv-versus-placebo comparison. For 250 mg, the interval runs from -2.089 to 5.503; for 375 mg, from -3.359 to 4.583; and for 500 mg, from -3.711 to 4.566. Thus, the estimates do not pin down a single direction of difference.

In general, a confidence interval is a range generated by a method that, under repeated use and its assumptions, would cover the target parameter at the stated frequency. It is not a range containing a specified probability that the true effect lies within it after the data have been observed. The 95% label describes the procedure’s long-run coverage, not certainty about an individual result.

The intervals’ span also matters: they include values on both sides of zero, so the data are compatible with some possible advantage for tirasemtiv and some possible advantage for placebo. The estimates are not precise enough to rule out all potentially relevant differences. The registry record does not report a clinically important difference threshold, so the confidence intervals cannot be classified against such a threshold from the registry information.

Standard errors for the arm-level least-squares means are reported, but those are not confidence intervals for the difference. The sponsor’s reported confidence intervals for the group comparisons are the more direct measure of precision for the randomized contrasts. The recalculated intervals are approximate and unadjusted; the sponsor’s model-based intervals should take precedence when interpreting the primary analysis.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For continuous outcomes, the figures are participants per arm. For the time-to-event outcome planning calculations, they are total numbers of events. The figures use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is the stated fraction of the observed effect: 100%, 75% or 50%.

The 80% power column describes a planned study size that, under those assumptions, would have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column describes a higher planned chance of detecting that same effect, and therefore generally requires a larger study size. These are planning concepts, not guarantees about any particular future study. This is not observed power.

Smaller effects require more participants or, for time-to-event planning, more events to distinguish the effect from random variation under the stated assumptions. That is why the planning requirements increase when the target is reduced from the full observed effect to 75% or 50% of it. Very small observed effects can produce especially large planning figures. The illustrations do not establish what effect is clinically worthwhile, and they should not be read as a retrospective explanation of why the original trial enrolled its participants. The original design assumptions and sample-size justification are not reported in the registry record.

The assumptions simplify planning. Actual requirements can differ with the final analysis method, allocation, outcome variability, event accrual, missing information and the effect researchers consider important. For time-to-event outcomes, the planning figures refer to total events, not participants per arm. These distinctions are essential when interpreting the labels and comparing figures across outcomes.

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 = 1.706; pooled standard deviation σ = 16.904.
2. n = 2 × (1.96 + 0.842)² × 16.904² / 1.706² = 1,541.2, rounded up to 1,542 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 <- 1.706                      # observed difference in means
sigma <- 16.9037424225946                     # 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(2496767)
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 = 1,542 (80% power), 2,064 (90% power)
 75% of observed effect: n per arm = 2,740 (80% power), 3,668 (90% power)
 50% of observed effect: n per arm = 6,165 (80% power), 8,253 (90% power)
power.t.test: 1542.1 
Simulated power at n = 1,542 per arm: 0.804 (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 sponsor’s primary analysis is a repeated-measures mixed model, reported as a least-squares mean difference with a 95% confidence interval and p-value. Those results are the relevant registered inferential analyses. The simple recalculations use the posted arm-level estimates and standard errors, with approximate pooled variability, to make unadjusted comparisons. They are not a reconstruction of the sponsor’s model.

The two approaches produce close estimates for the primary contrasts. For example, the recalculated difference for 250 mg is 1.706, while the sponsor reports 1.707; the corresponding recalculated and sponsor-reported intervals are also similar. The recalculated estimates for 375 mg and 500 mg are 0.612 and 0.427, compared with sponsor estimates of 0.612 and 0.428. This agreement is a useful consistency check, but does not make the methods interchangeable.

The recalculated p-values are unadjusted and arise from a simplified comparison. The sponsor’s p-values arise from the stated repeated-measures analysis and should be used when describing the trial’s own results. The registry record does not identify a discrepancy between the recalculations and the reported results. Neither analysis provides a statistically clear primary difference from placebo, and the model-based sponsor results remain the principal interpretation.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 7 outcome measures and 21 analyses. The primary endpoint is clear, but multiple secondary outcomes and treatment comparisons raise a multiplicity issue: the more hypotheses examined, the greater the chance that at least one result will appear notable by chance. The registry record does not report whether the analysis plan used a family-wise error procedure, a hierarchical testing sequence, or another adjustment for multiple comparisons. The degree to which secondary p-values were confirmatory therefore cannot be determined from the registry record.

The Full Analysis Set is described as participants who received at least one dose during the randomized double-blind placebo-controlled phase and had at least one post-randomization efficacy assessment. This defines the population underlying the posted primary arm results. The registry record does not report the number excluded from this set, reasons for exclusion, or a separate intention-to-treat analysis. The total enrollment and the primary endpoint analysis counts answer different questions and should not be treated as interchangeable.

Missing data are particularly relevant for a repeated-measures endpoint over time. The mixed-model method is reported, but the assumptions about missing measurements, the amount and pattern of missingness, and sensitivity analyses are not reported in the registry record. Without these details, it is not possible to assess how departures from the model’s missing-data assumptions might affect the primary estimate.

The registry record also does not report the full statistical analysis plan, interim analysis procedures, stopping rules, covariate adjustments or multiplicity strategy. These omissions do not invalidate the posted results, but they limit independent assessment of prespecification and robustness. The reported estimates and their uncertainty remain interpretable as registry results, while stronger claims about the analysis strategy require information not reported in the registry record.

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: dysphagia (9.5%), respiratory failure (4.8%), weight decreased (4.0%), pneumonia (2.9%), amyotrophic lateral sclerosis (2.9%).

The safety record separates participants in the open-label lead-in, the double-blind placebo-controlled groups and double-blind withdrawal groups. It reports the number at risk and the number affected by serious adverse events, other adverse events and deaths within each listed group. For the main placebo-controlled groups, serious adverse events were reported for 53 participants in placebo, 30 in the 250 mg group, 30 in the 375 mg group and 32 in the 500 mg group. Other adverse events were reported for 182, 125, 125 and 125 participants in those respective groups.

These are counts, not estimates of causal treatment effects. The groups differ in size, and the registry record presents distinct study periods and group definitions. The open-label lead-in and withdrawal groups should not be pooled mentally with the randomized placebo-controlled comparisons. Deaths are also reported separately; the registry lists 17 in the placebo group, 8 in the 250 mg group, 10 in the 375 mg group and 8 in the 500 mg group.

The listed serious-event terms include dysphagia (9.5%), respiratory failure (4.8%), weight decreased (4.0%), pneumonia (2.9%), amyotrophic lateral sclerosis (2.9%) and pulmonary embolism (2.4%). The record does not establish from these descriptive entries whether a particular event was caused by study treatment. The available safety figures should be read as reported events within their stated groups, not as a complete causal comparison or personalized risk estimate.

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

The results establish what the registry reports about this trial’s measured outcomes: mean percent predicted SVC declined from baseline in all randomized groups, and the Week 24 model-based comparisons did not identify a statistically clear difference between any tirasemtiv dose group and placebo. The confidence intervals include zero and permit differences in either direction. The findings are therefore uncertain rather than proof that the groups had exactly the same outcome.

The results do not establish that tirasemtiv had no effect, that a difference of clinical importance is impossible, or that the treatment is equivalent to placebo. Those conclusions would require appropriately designed analyses, a clinical importance threshold and sufficiently precise estimates. A non-significant p-value is not a test of equivalence. The registry record does not report a clinically important difference threshold for the primary endpoint.

Nor does the primary endpoint capture every aspect of ALS or respiratory health. It is a specific spirometric measure at a defined follow-up point. Secondary outcomes cover other measures, but several results are not reported in the registry record and the multiplicity strategy is not reported. Conclusions should therefore remain tied to the endpoint, population, time point and analysis actually described.

The study’s randomized, masked, placebo-controlled design supports a comparative interpretation of the assigned groups, subject to the analysis assumptions and the limitations of the available record. It does not make every observed event attributable to the assigned treatment, and descriptive safety counts are not causal estimates. The posted evidence is best read as an uncertain primary comparison, with no clear statistical separation from placebo at Week 24, alongside secondary and safety information that requires its own cautious interpretation.

18. Why This Trial Matters Statistically

This trial illustrates the distinction between the direction of a point estimate and the strength of evidence for a difference. Each primary tirasemtiv estimate is positive relative to placebo, but each confidence interval spans zero. A reader who attends only to the point estimates could overstate the evidence; a reader who treats non-significance as proof of no effect could overstate it in the other direction. The intervals communicate that the estimates remain uncertain.

It also illustrates why the registered analysis method matters. The sponsor used a repeated-measures mixed model for a longitudinal endpoint, whereas the recalculations are simple unadjusted comparisons from summary statistics. Their close agreement is reassuring as a numerical cross-check, but the model-based sponsor estimates are the relevant trial analyses because they use the stated repeated-measures approach.

The study further shows how endpoint choice and follow-up shape interpretation. Week 24 SVC, 48-week respiratory-domain scores and time-to-event outcomes are related but not interchangeable. Secondary analyses can add context, yet multiple comparisons and incomplete reporting reduce the weight that can be placed on isolated results. Clear reporting of analysis populations, missing-data assumptions, model details and multiplicity plans is important for judging how robust a conclusion is.

Finally, planning illustrations based on observed effects are not evidence that the completed trial was adequately or inadequately powered. Their size depends strongly on the effect assumed for a future study. The original trial’s sample-size justification is not reported in the registry record. Keeping planning calculations separate from observed results prevents retrospective power claims from being mistaken for evidence about the treatment effect.

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 registry record leaves important aspects of the design and analysis unspecified. It does not report the original sample-size justification, stratification factors, masked roles or full statistical analysis plan. It also does not give the mixed model’s covariance structure, covariate adjustments or assumptions for missing repeated measurements. Those omissions constrain assessment of the analysis choices and robustness.

The primary result applies to the stated Full Analysis Set, not automatically to every participant enrolled. The record defines the set using receipt of study drug and availability of a post-randomization efficacy assessment, but does not report exclusions, reasons for missing assessment or sensitivity analyses. The degree to which missing data could affect the estimated changes cannot be evaluated from the registry entries alone.

The posted secondary findings are incomplete relative to the listed outcomes and analyses. The record lists 7 outcome measures and 21 analyses, but not all corresponding results are present in the reported information. The multiplicity strategy is not reported, which weakens interpretation of individual secondary p-values. A complete protocol and analysis plan would be needed to distinguish confirmatory analyses from exploratory ones.

The dose descriptions for the 375 mg and 500 mg groups are incomplete in the registry record, and do not establish all treatment details over the full study period. Safety information includes lead-in, randomized treatment and withdrawal groups, which are not directly interchangeable. Finally, the registry record provides no clinical-importance threshold for the primary endpoint. The statistical intervals therefore cannot, by themselves, show whether any compatible difference would be meaningful to patients.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ventilatory Investigation of Tirasemtiv and Assessment of Longitudinal Indices After Treatment for a Year — NCT02496767.
• Registry record last updated 2020-09-09; status last verified 2020-08.
• Results first posted 2020-06-19.
• 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

The registry record describes a completed phase 3 randomized, triple-masked, parallel-group, placebo-controlled study of tirasemtiv in ALS, with enrollment of 744. The primary endpoint was change from baseline to Week 24 in percent predicted SVC, analyzed in a Full Analysis Set.

Mean changes were negative in the placebo and all tirasemtiv groups. Sponsor-reported repeated-measures mixed-model comparisons did not show a statistically clear difference from placebo; each 95% confidence interval included zero. Recalculations from the posted summary statistics were similar but remain unadjusted approximations.

Secondary outcomes address respiratory function, muscle strength and clinical events, though not all listed results are reported. The registry provides descriptive adverse-event counts across several study groups. Analysis-plan details, multiplicity procedures, missing-data assumptions and the original sample-size justification are not reported in the registry record.