Multi-arm Optimization of Stroke Thrombolysis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Multi-arm Optimization of Stroke Thrombolysis (NCT03735979), a randomized phase 3 study. The primary outcome is 90-day Utility Weighted Modified Rankin Scores (UW-mRS).

2. Clinical Question

3. Trial Design

MOST (NCT03735979) was a phase 3 randomized, double-masked, parallel-group trial. Its official title describes an adaptive, multi-arm adjunctive-thrombolysis efficacy trial in ischemic stroke. The registry lists Washington University School of Medicine as sponsor and the condition as acute ischemic stroke. The trial status is completed. The recorded start date is 2019-10-15, and primary completion is recorded as 2023-12-01.

There were three treatment groups: argatroban, eptifibatide, and placebo. Both active treatments were studied as additions to standard-of-care thrombolysis; endovascular thrombectomy could be provided per usual care. The registry reports enrollment of 514. Posted primary-outcome group summaries are 59 for argatroban, 227 for eptifibatide, and 228 for placebo. The primary analysis population is identified as intention-to-treat.

The adaptive feature is part of the official trial title, but the specific adaptation rules, decision points, and any changes made during the trial are not reported in the registry record. The allocation ratio and the trial's original sample-size assumptions are also not reported in the registry record. The presence of an adaptive design label alone does not establish how adaptations were implemented or whether any occurred.

The registry describes 90-day utility-weighted modified Rankin scores as the primary outcome. Other listed outcomes cover neurological status at 24 hours, 90-day disability and health status, and thrombectomy-related measures. The record lists 13 outcome measures and identifies 8 secondary outcomes. How missing observations were handled, and whether all randomized participants contributed data to each outcome, is not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat

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 90-day Utility Weighted Modified Rankin Scores (UW-mRS), measured over 90 days after randomization.

The primary endpoint was the utility-weighted modified Rankin score 90 days after randomization. The modified Rankin scale is an ordinal measure with levels from 0, meaning no symptoms, to 6, meaning death. For the primary analysis, each level was assigned a patient-centered utility weight, and higher weighted scores indicate a better outcome. The endpoint was analyzed as a mean with a standard deviation, rather than as a simple count at a single Rankin threshold.

Utility weighting expresses differences across disability states on a scale intended to reflect how patients value those states. That can make a mean comparison sensitive to the distribution of outcomes across the full scale, rather than only to whether a participant falls above or below one chosen cut point. A mean can therefore summarize an overall shift in weighted outcome, while obscuring the different patterns of disability that produce that mean. The posted group means and standard deviations do not show the full distribution across the Rankin levels.

A 90-day disability outcome provides a fixed follow-up point for comparing functional status after stroke. The registry identifies the primary analysis population as intention-to-treat, which generally means participants are analyzed according to randomized group. The detailed handling of incomplete 90-day assessments is not reported in the registry record.

7. Results Posted in the Registry

• Argatroban: mean 5.20 versus 6.80 on control; difference -1.60 (95% CI -2.62 to -0.58), standardized effect d = -0.51; z-test p = 0.002.
• Eptifibatide: mean 6.30 versus 6.80 on control; difference -0.50 (95% CI -1.07 to 0.07), standardized effect d = -0.16; z-test p = 0.086.

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.

Percentage of Participants With NIHSS Less Than or Equal to 2 at 24 Hours

• 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:
  • Argatroban: 23.7% (14/59) versus 39.0% (89/228) on control; risk difference -15.3 percentage points (95% CI -27.9 to -2.7), risk ratio 0.61 (0.37–0.99); unadjusted two-proportion z-test p = 0.029.
  • Eptifibatide: 37.0% (84/227) versus 39.0% (89/228) on control; risk difference -2.0 percentage points (95% CI -10.9 to 6.9), risk ratio 0.95 (0.75–1.20); unadjusted two-proportion z-test p = 0.655.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Argatroban than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Eptifibatide and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to 24-hour NIHSS

• 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 deviations.
• Result:
  • Argatroban: mean -5.10 versus -6.30 on control; difference 1.20 (95% CI -1.33 to 3.73), standardized effect d = 0.16; z-test p = 0.353.
  • Eptifibatide: mean -6.10 versus -6.30 on control; difference 0.20 (95% CI -1.20 to 1.60), standardized effect d = 0.03; z-test p = 0.780.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Argatroban 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 Eptifibatide and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With 90-day mRS 0 or 1 (or Return to Their Historical mRS)

• 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:
  • Argatroban: 23.7% (14/59) versus 40.4% (92/228) on control; risk difference -16.6 percentage points (95% CI -29.2 to -4.0), risk ratio 0.59 (0.36–0.95); unadjusted two-proportion z-test p = 0.018.
  • Eptifibatide: 36.1% (82/227) versus 40.4% (92/228) on control; risk difference -4.2 percentage points (95% CI -13.1 to 4.7), risk ratio 0.90 (0.71–1.13); unadjusted two-proportion z-test p = 0.354.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Argatroban than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Eptifibatide and the control. The interval gives the range of effects that remain compatible with the data.

The registered secondary outcomes cover early neurological status, changes in neurological status, 90-day disability and health status, and thrombectomy-related imaging scores. The posted secondary results include early NIHSS measures and a 90-day mRS threshold outcome. Across these outcomes, the unadjusted recalculations do not form a uniformly strong pattern of differences favoring an active adjunct. Several confidence intervals include no difference, while some argatroban comparisons have intervals that do not include zero. These findings are secondary to the prespecified primary outcome and should be understood alongside the sponsor's primary analysis, not as independent substitutes for it.

Secondary endpoints can help describe whether patterns in the primary outcome are accompanied by differences in other measures or at other follow-up points. They may also capture aspects of recovery not fully represented by a single utility-weighted mean. However, outcomes differ in scale, timing, and clinical meaning, so their effect estimates cannot simply be combined into one overall conclusion. A threshold outcome, for example, answers a different question from a mean change or a score on the full scale.

Unadjusted secondary results carry less weight when many outcomes and comparisons are examined. In general, the more hypotheses tested, the greater the chance that some results appear notable by chance alone. The registry does not report whether multiplicity adjustments were planned or applied, or how the secondary analyses were prioritized. The results therefore should not be treated as confirmatory evidence unless supported by the trial's full prespecified analysis plan.

Results for other listed secondary outcomes, including 90-day EQ-5D and thrombectomy-related modified TICI outcomes, are not reported in the registry record. The pattern across posted secondary results can add context, but the missing analysis details and incomplete set of posted outcome results limit what can be concluded about consistency across the full outcome program.

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

• Percentage of Participants With NIHSS Less Than or Equal to 2 at 24 Hours
• Change From Baseline to 24-hour NIHSS
• Percentage of Participants With 90-day mRS 0 or 1 (or Return to Their Historical mRS)
• Percentage of Participants With 90-day mRS 0, 1 or 2 (or Return to Their Historical mRS)
• 90-day mRS
• 90-day EQ-5D
• Pre-thrombectomy Modified TICI Score of 2B.
• Post-thrombectomy Modified TICI Score of 2B or 3

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous in the posted analysis: each participant's utility-weighted score contributes to a group mean, and the standard deviation describes variation among scores within that group. Comparing means gives an estimate of the average difference on the weighted scale. It does not show how many participants had a particular Rankin score or how outcomes were distributed across the scale.

What does a mean difference represent?

The recalculated mean difference is expressed as active treatment minus placebo. A negative estimate therefore means that the active-treatment group mean is lower than the placebo group mean on the posted scale. The estimate is a summary contrast; it is not an individual participant's change and does not indicate that every participant had an outcome in the same direction. The clinical meaning of a difference depends on the scale and on how the utility weights distinguish outcome states.

The recalculations use the posted group means, standard deviations, and group sizes to make simple unadjusted comparisons. They do not account for any covariates, stratification factors, adaptive-design features, or other modeling choices unless those are explicitly incorporated. The registry does not give enough detail to determine the full analysis model used for the sponsor's reported results. The recalculated standard errors and intervals are therefore best read as an independent, summary-statistic-based comparison, not as a reproduction of the sponsor's analysis.

What does the confidence interval add?

A confidence interval describes the range of estimates that are reasonably compatible with the data under the calculation method and its assumptions. It conveys uncertainty as well as the direction and size of an estimated difference. Its width reflects precision: a narrower interval indicates less uncertainty in the estimated contrast, while a wider interval indicates more. The interval does not assign a probability that the true effect lies within its particular endpoints.

For the argatroban recalculation, the 95% confidence interval is wholly below zero. For the eptifibatide recalculation, the interval extends across zero. These are statements about the unadjusted recalculated intervals. They should not be substituted for the sponsor's Bayesian analyses, which are reported without confidence limits in the registry record. An interval and a p-value also answer related but different questions: the interval shows a range of compatible estimates, while the p-value measures how unusual the observed data would be under a specified null model and its assumptions.

What does a p-value say?

A p-value is not the probability that a treatment is effective, nor is it a measure of clinical importance. Its interpretation depends on the statistical model and the hypothesis being tested. The unadjusted recalculated p-values are attached to simple comparisons of means. The sponsor p-values are attached to analyses identified as Bayesian superiority analyses, but their exact construction is not reported. The p-values from these approaches should not be compared as if they necessarily came from identical models.

The registry reports standard deviations for the primary outcome but no group-specific confidence limits. The spread of individual scores matters because greater variability generally makes a mean harder to estimate precisely. The observed group sizes also differ, and a smaller group can contribute less precise information about its mean than a larger group, all else being equal. This is a general statistical principle, not an additional result about the trial.

Why can outcome shape matter?

The modified Rankin scale is ordinal: its levels have an order, but adjacent levels need not represent equal clinical distances. Utility weights transform the levels to a weighted score for the primary analysis. A comparison of means then relies on that weighted scale. It can be useful for summarizing overall outcome, but it does not preserve every detail of the underlying ordinal distribution. The full distribution by Rankin level and the sponsor's model specification are not reported in the registry record.

The trial title describes an adaptive design, but no adaptation procedure is reported. Adaptive designs can use prespecified rules to modify aspects of a trial based on accumulating information; the actual rules and consequences depend on the protocol. Without those details, no claim can be made about adaptation, interim looks, error-rate control, or how the final estimates account for adaptive decisions. The registry's description of the trial as adaptive is not itself a statistical-methods specification.

General considerations such as multiplicity are also relevant when many outcomes or comparisons are examined. Testing multiple hypotheses can increase the chance of a nominally notable result under a setting where none of the hypotheses is true. Whether and how the sponsor controlled multiplicity is not reported in the registry record. The secondary outcomes should therefore be read as additional descriptive and inferential evidence, not as independent confirmation without regard to the analysis plan.

11. Confidence Intervals and Precision

The recalculated mean difference for argatroban versus placebo is -1.6, with a 95% confidence interval from -2.621 to -0.579. This interval excludes zero under the unadjusted recalculation and is consistent with a lower mean utility-weighted score in the argatroban group. The interval still spans a range of possible differences; the point estimate alone should not be mistaken for exact knowledge of the contrast.

For eptifibatide versus placebo, the recalculated difference is -0.5, with a 95% confidence interval from -1.07 to 0.07. Because the interval includes zero, the recalculation does not rule out no mean difference, and it also includes values on either side of zero. Its width indicates that the summary-statistic comparison leaves appreciable uncertainty about the contrast.

Precision depends on the amount of information and the variability in the outcome, among other factors. The posted primary-outcome standard deviations are 3.7 for argatroban, 3.2 for eptifibatide, and 3.0 for placebo. The group sizes differ, with 59 in the argatroban group, 227 in the eptifibatide group, and 228 in the placebo group. Those details help explain why the comparisons do not have identical precision, but they do not by themselves describe every feature of the sponsor's analysis.

The confidence intervals belong to the recalculations, not the reported sponsor analyses. The sponsor posterior mean differences are -1.51 and -0.5, and confidence limits are not reported for either. The discrepancy flag means the sponsor's analysis takes precedence. Accordingly, the recalculated intervals are useful for understanding uncertainty in a simple unadjusted contrast, but should not be presented as uncertainty intervals from the sponsor's Bayesian model.

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 planning illustrations are participants per arm, not total events. They use the observed effect as a starting point and show hypothetical requirements for detecting the stated fraction of that effect. For continuous outcomes, the illustrations are based on a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The trial's original design assumptions are not reported in the registry record, so these illustrations should not be read as the trial's planned enrollment target or as a reconstruction of its adaptive design.

The 80% power column gives the number of participants per arm in a hypothetical design that would have an 80% chance of detecting the specified effect if the planning assumptions and effect were correct. The 90% power column gives the corresponding per-arm number for a 90% chance. These are prospective planning concepts. The illustrations are not observed power.

Rows for planning for 100% of the observed effect use the full observed contrast as the hypothetical target; rows for planning for 75% or 50% of the observed effect use smaller targets. A smaller effect is harder to distinguish from random variation, so it generally requires more participants to reach the same planned power. This pattern is visible across the planning illustrations, including comparisons where the observed difference is small. The estimates are sensitive to the observed effect used as a starting point: if that observed effect is unstable or not representative of a future study, the planning illustration may not be a reliable guide to future requirements.

Binary outcomes use the posted risk difference as the observed contrast for their own illustrations. The same per-arm reading applies to these planning figures. These calculations do not incorporate additional assumptions about attrition, allocation changes, multiplicity, adaptive rules, or other features that may matter to an actual study. Such details are not reported in the registry record.

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 = -1.600; pooled standard deviation σ = 3.155.
2. n = 2 × (1.96 + 0.842)² × 3.155² / -1.600² = 61.0, rounded up to 62 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 <- -1.6                      # observed difference in means
sigma <- 3.15506832578169                     # 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(3735979)
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 = 62 (80% power), 82 (90% power)
 75% of observed effect: n per arm = 109 (80% power), 146 (90% power)
 50% of observed effect: n per arm = 245 (80% power), 327 (90% power)
power.t.test: 62 
Simulated power at n = 62 per arm: 0.800 (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 reports a sponsor Bayesian superiority analysis for each active-treatment comparison with placebo. The posterior mean difference for argatroban is -1.51 with p = 0.002; for eptifibatide it is -0.5 with p = 0.04. Confidence limits and a confidence level are not reported for either sponsor estimate. The registry does not report enough model detail to reconstruct these analyses or to explain how the p-values were calculated.

The separate recalculations compare the posted group means and standard deviations using simple unadjusted methods. They give -1.6 for argatroban versus placebo, with a 95% confidence interval from -2.621 to -0.579 and p = 0.002, and -0.5 for eptifibatide versus placebo, with a 95% confidence interval from -1.07 to 0.07 and p = 0.086. The recalculation and sponsor estimates are not identical in all respects, and their uncertainty summaries are not the same kind of analysis.

The record flags a discrepancy. In that situation, the sponsor's own analysis takes precedence; the recalculations are informative checks based on posted summaries, not replacements for the sponsor's analysis. The difference in the eptifibatide p-values underscores that analytic method and assumptions can affect statistical conclusions. Without the sponsor's full model, prior choices, and analysis plan, the discrepancy cannot be resolved from the registry record alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome, multiple secondary outcomes, and comparisons of two active treatments with placebo. Whenever several outcomes or contrasts are analyzed, multiplicity is a statistical concern: the chance of observing at least one apparently notable result can increase as the number of hypotheses grows. This general concern does not establish that any particular result is false; it means that p-values and confidence intervals should be interpreted in light of the analysis plan and the number of planned tests.

Whether the trial used a multiplicity adjustment, hierarchical testing, a gatekeeping procedure, or another approach is not reported in the registry record. The protocol's hypothesis-testing sequence, any prespecified primary comparison strategy, and the treatment of secondary outcomes are also not reported. The trial's adaptive design label makes details of planned decision rules relevant, but the registry does not describe interim analyses, adaptation rules, or any statistical adjustment associated with adaptations. No specific procedure should be inferred.

The primary analysis population is identified as intention-to-treat. This label generally indicates that participants are analyzed in their randomized groups, but it does not specify how missing outcome measurements, deviations from treatment, or unavailable assessments were handled. The number of participants with observed primary outcomes by group, the amount and pattern of missing data, imputation methods, sensitivity analyses, and reasons for missingness are not reported in the registry record.

Missingness matters because an analysis based only on observed outcomes can be misleading if participants without measurements differ systematically from those with measurements. Statistical methods can address some missing-data problems, but their validity depends on assumptions and available information. Without the missing-data methods and sensitivity analyses, the robustness of the primary and secondary comparisons to incomplete follow-up cannot be assessed from the registry record.

These omissions limit independent evaluation of the analysis strategy. They do not demonstrate that the sponsor failed to plan or perform such analyses; they mean the details are 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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: low frequency saes (27.1%), ischaemic stroke (8.5%), respiratory failure (6.8%), cardiac arrest (5.1%), atrial fibrillation (3.4%).

The registry reports serious adverse events for 26 of 59 participants in the argatroban group, 85 of 227 in the eptifibatide group, and 78 of 228 in the placebo group. Other adverse events are reported for 12 of 59, 42 of 227, and 33 of 228 participants, respectively. Deaths are listed for 13 participants in the argatroban group, 25 in the eptifibatide group, and 17 in the placebo group.

These counts describe the registry's reported event categories and group denominators. They do not establish that an event was caused by the assigned treatment, and the registry record does not provide a treatment-causality assessment or a detailed account of event timing. The listed serious adverse-event terms include “Low frequency SAEs” at 27.1%, ischaemic stroke at 8.5%, respiratory failure at 6.8%, cardiac arrest at 5.1%, atrial fibrillation at 3.4%, and gastrointestinal haemorrhage at 3.4%. The registry does not explain the denominator or coding details for these term percentages in the information reported.

Safety counts should be read descriptively and in context with follow-up, event definitions, exposure, and the methods used to collect and classify events. Those details are not fully reported in the registry record. The figures alone do not establish comparative safety or explain differences between groups.

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

The primary outcome is a weighted summary of disability status 90 days after randomization. The posted group means are lower in both active-treatment groups than in the placebo group, while the sponsor's Bayesian analyses report superiority comparisons with negative posterior mean differences. The simple recalculation also gives a negative mean difference for each active group, but its interval for eptifibatide includes zero. Because a discrepancy is flagged, the sponsor's own analysis takes precedence over the recalculation.

These results do not establish the full distribution of outcomes across modified Rankin levels. Nor do they describe whether particular subgroups had different outcomes, how missing follow-up affected the estimates, or how results might vary under other trial populations or treatment settings. The registry record does not report the sponsor's detailed model specification, multiplicity strategy, missing-data handling, or adaptive-design rules. Those omissions constrain independent assessment of the analysis and its assumptions.

A statistically notable result is not by itself a measure of clinical importance. The meaning of a difference on this utility-weighted scale depends on the utility assignments and on the way score differences relate to outcomes that matter to patients. The record states that higher scores indicate better outcomes, but the posted means and contrast estimates do not capture every aspect of disability, recovery, or treatment burden.

The secondary results offer additional context but do not replace the primary outcome. They include different measures and follow-up periods, and multiple comparisons can make unadjusted findings less definitive. Safety counts are also descriptive; they do not alone establish treatment causation or a comparative safety conclusion.

Overall, the registry record describes a randomized comparison of two adjunctive treatments with placebo and reports the primary outcome and selected additional results. It does not provide enough detail to resolve every analytic uncertainty or to infer that the findings apply beyond the studied setting. The results should be understood as evidence from this trial record, not as medical advice or a universal prediction of an individual's outcome.

18. Why This Trial Matters Statistically

MOST illustrates why analysis choices matter in a multi-arm clinical trial. The same posted primary-outcome summaries can be examined with a simple unadjusted recalculation or through the sponsor's Bayesian analysis, and the registry flags a discrepancy between those approaches. The contrast in reported results, particularly for eptifibatide, shows why readers need to know which estimate comes from the sponsor's prespecified analysis and which is an independent recalculation. The sponsor analysis takes precedence when the record flags a discrepancy.

The endpoint also raises an important measurement issue. A utility-weighted mean compresses an ordinal disability scale into a summary score. This supports an overall comparison, but it cannot display the full pattern of outcomes at each scale level. Reading the mean alongside other outcomes and understanding the weighting scheme are important for interpreting what a difference represents.

The trial's multi-arm and adaptive description makes transparent design and analysis reporting especially useful. Readers need the allocation rules, adaptation procedures, multiplicity strategy, and analysis plan to understand how the final comparisons were selected and evaluated. Those details are not reported in the registry record. Their absence limits independent evaluation without proving that the underlying trial procedures were deficient.

Finally, the secondary outcomes and safety counts demonstrate the distinction between descriptive signals and confirmatory evidence. Multiple outcomes can provide a broader view, but unadjusted results require caution, and adverse-event counts do not identify causation. Taken together, the record offers a concrete example of why effect estimates, precision, analysis methods, and reporting completeness should be considered together rather than reducing a trial to one p-value.

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 does not report the specific rules for the adaptive design, whether interim analyses occurred, or how any adaptive decisions were incorporated into the final analyses. It also does not report the original sample-size assumptions, allocation ratio, or detailed statistical analysis plan. These omissions prevent an independent assessment of the design's decision process and of how the sponsor's analyses were specified before results were known.

The primary outcome is a utility-weighted mean derived from an ordinal scale. The record gives the direction of the scale and states that higher scores are better, but the posted summaries do not show the distribution of participants across the modified Rankin levels. The utility weights are listed in the endpoint description, but the registry's weight string contains a formatting irregularity. The full outcome distribution and any sensitivity analyses using alternative scoring approaches are not reported in the registry record.

The record reports a discrepancy between the sponsor's Bayesian results and the simple unadjusted recalculations. Sponsor confidence limits, model details, and prior assumptions are not reported, so the reported Bayesian analyses cannot be reproduced from the registry information alone. The recalculations do not account for unreported covariates or design features and should not be interpreted as corrected sponsor estimates.

Missing-data methods, outcome completeness by group, and sensitivity analyses are not reported. The registry also does not report whether secondary-endpoint multiplicity was controlled. Only selected secondary results are included in the detailed outcome information, while results for other listed outcomes are not reported in the registry record. Safety event definitions, causality assessments, and event timing are not described in detail. These limitations affect how fully the results can be independently appraised.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Multi-arm Optimization of Stroke Thrombolysis — NCT03735979.
• Registry record last updated 2025-02-07; status last verified 2025-01.
• Results first posted 2024-11-19.
• 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

NCT03735979, Multi-arm Optimization of Stroke Thrombolysis, is a completed phase 3 randomized, double-masked, parallel-group trial sponsored by Washington University School of Medicine. It enrolled 514 participants with acute ischemic stroke and compared argatroban and eptifibatide with placebo as adjuncts to standard-of-care thrombolysis. The primary endpoint was the 90-day utility-weighted modified Rankin score, with higher scores indicating a better outcome.

The registry reports Bayesian sponsor superiority analyses and group-level outcome summaries. Simple unadjusted recalculations are also available, but a discrepancy is flagged and the sponsor's own analysis takes precedence. Details of the adaptive procedures, multiplicity strategy, missing-data handling, original design assumptions, and full sponsor model are not reported in the registry record. Secondary outcomes and adverse-event counts provide additional descriptive context but do not resolve these analysis limitations.