POSITIVE Stroke Clinical Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for POSITIVE Stroke Clinical Trial (NCT01852201), a randomized na study. The primary outcome is Rate of Good Functional Outcomes Measured by Modified Rankin Score (mRS).

2. Clinical Question

This is a clinical question about a specific treatment window and imaging-selected population, rather than all patients with ischemic stroke. The registry record identifies ischemic stroke as the condition and describes participants who were not eligible for, or did not respond to, IV-tPA. It does not report enough participant characteristics to determine how closely the enrolled group represents other stroke populations or clinical settings.

3. Trial Design

The POSITIVE Stroke Clinical Trial was a randomized study with an open-label design: allocation was randomized, and masking was listed as none. The record classifies its model as factorial, but the factors, their levels, and how any factorial structure relates to the two posted treatment arms are not reported in the registry record. The listed arms are best medical therapy and endovascular treatment. Enrollment was 33, with 21 participants in the best medical therapy arm and 12 in the endovascular treatment arm for the primary outcome.

The target clinical setting was acute ischemic stroke in patients who were ineligible for or refractory to IV-tPA, had appropriate imaging selection, and could receive mechanical thrombectomy within 6-12 hours of symptom onset. The record describes best conventional treatment as determined by the attending stroke physician. The endovascular procedure could be performed under general anesthesia or conscious sedation, according to the treating physician. The record also describes general medical management according to AHA/ASA guideline in both arms.

The study started in 2013-09, and primary completion is recorded as 2017-05-31. Its status is terminated. The reason for termination, details of the factorial design, allocation concealment, and the trial’s original sample-size justification are not reported in the registry record. The listed phase is NA.

Randomization is intended to support a fair comparison by balancing participant characteristics across treatment groups on average. With only 33 participants, however, chance differences between groups can remain, and estimates may be imprecise. The open-label design means participants and treating clinicians were not masked to assignment. Whether outcome assessors were masked is not reported in the registry record. That distinction matters because the primary outcome involves assessment of disability, although a standardized scale can help define the outcome consistently.

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

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 Rate of Good Functional Outcomes Measured by Modified Rankin Score (mRS), measured over 90 days.

The posted primary outcome is the percentage of participants with a good functional outcome at 90 days, defined as a modified Rankin Scale (mRS) score from 0-2. The mRS measures disability or dependence in daily activities after stroke or another cause of neurological disability. Its range is 0-6, with 0 representing the highest function and no symptoms and 6 representing death. A threshold of 0-2 turns this ordered scale into a binary outcome: each participant is classified as having either a good functional outcome or not meeting that threshold.

In general, a global disability scale is used because it captures more than a single symptom or impairment and can summarize a person’s overall level of function. A binary threshold can make the result more directly interpretable as the proportion reaching a defined outcome. The trade-off, in general, is that reducing an ordered scale to two groups loses information about differences within each group and about how far participants are from the threshold.

The registry record’s primary endpoint title and description define the result as the percentage with mRS 0-2 at 90 days. Its brief summary separately describes 90-day global disability analyzed using raw mRS scores and refers to the overall mRS distribution as a secondary endpoint. This difference in wording is relevant when interpreting what the primary analysis was intended to test. Details of how the raw scores were analyzed are not reported in the registry record.

7. Results Posted in the Registry

• Endovascular Treatment: 75.0% (9/12) versus 42.9% (9/21) on control; risk difference 32.1 percentage points (95% CI -0.2 to 64.5), risk ratio 1.75 (0.97–3.16); unadjusted two-proportion z-test p = 0.074.

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 Mortality at 30 Days

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Endovascular Treatment: 0.0% (0/12) versus 11.8% (2/17) on control; risk difference -11.8 percentage points (95% CI -27.1 to 3.6); unadjusted two-proportion z-test p = 0.218.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Endovascular Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Mortality at 90 Days

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Endovascular Treatment: 8.3% (1/12) versus 19.0% (4/21) on control; risk difference -10.7 percentage points (95% CI -33.7 to 12.2), risk ratio 0.44 (0.06–3.48); unadjusted two-proportion z-test p = 0.409.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Endovascular Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With SAE's Related to a Thrombectomy Procedure

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Endovascular Treatment: 8.3% (1/12) versus 0.0% (0/21) on control; risk difference 8.3 percentage points (95% CI -7.3 to 24.0); unadjusted two-proportion z-test p = 0.179.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Endovascular Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The numerical secondary results cover mortality at 30 days and 90 days, and serious adverse events related to a thrombectomy procedure. The registry lists additional secondary outcomes, including overall mRS distribution, good functional recovery, neurological deterioration with intracranial hemorrhage, and arterial revascularization, but their numerical results are not reported in the registry record. No reported analyses are listed for the posted secondary outcomes.

Across the secondary comparisons with numerical results, the posted confidence intervals are broad and include the null value on the risk-difference scale. The unadjusted p-values also do not provide strong evidence against the null under a conventional 0.05 threshold. This overall pattern is consistent with substantial uncertainty in a trial with small denominators; it should not be treated as evidence that the groups are equivalent.

The secondary outcomes address different aspects of the study: mortality reflects a serious clinical outcome, and procedure-related serious adverse events describe harms associated with thrombectomy procedures. These outcomes complement the 90-day functional endpoint but do not replace it. They may help describe the broader outcome pattern, yet they involve fewer participants and, for some outcomes, few events. Estimates based on sparse events are especially sensitive to individual observations.

In general, multiple outcome comparisons create more opportunities for chance findings when each is assessed separately. Unless a multiplicity strategy is specified, unadjusted secondary p-values should be interpreted as exploratory rather than as a collection of independent confirmatory tests. A multiplicity adjustment and a hierarchy for testing secondary outcomes are not reported in the registry record. For that reason, the secondary findings carry less inferential weight than a prespecified primary analysis, and they should be considered in the context of the primary result rather than as separate definitive conclusions.

The registry record does not provide numerical results for all listed secondary outcomes, so the pattern cannot be assessed across every planned measure. In particular, the available record does not show the overall mRS distribution or numerical findings for the listed revascularization and neurological deterioration outcomes. Those absences limit a fuller assessment of how the functional and safety outcomes align.

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

• Percentage of Participants in the 6-12 hr Cohort With Global Disability as Assessed by the Modified Rankin Score (mRS)
• Percentage of Participants in the 6-12hr Cohort With Good Functional Recovery as Assessed by the Modified Rankin Scale (mRS)
• Percentage of Participants Mortality at 30 Days
• Percentage of Participants Mortality at 90 Days
• Percentage of Participants With ICH (Intracranial Hemorrhage) With Neurological Deterioration (NIHSS Worsening >4).
• Percentage of Participants With SAE's Related to a Thrombectomy Procedure
• Arterial Revascularization Measured by TICI 2b or 3 Following Device Use
• Percentage of Patients With Serious Adverse Events (SAEs) Related to Thrombectomy Device.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary as posted: each participant either had an mRS score of 0-2 at 90 days or did not. For such an outcome, the arm-specific percentage describes the proportion meeting the threshold among participants included in that outcome summary. The registry gives 42.9% for best medical therapy and 75.0% for endovascular treatment, with denominators of 21 and 12. The posted counts meeting the threshold are 9 and 9, respectively.

What does the risk difference express?

In general, a risk difference subtracts the event proportion in one group from the event proportion in another, retaining the scale of absolute probability. The posted comparison is expressed as the endovascular treatment arm relative to best medical therapy. Its estimate is 0.321 and its 95% confidence interval is -0.002 to 0.645. Positive values on this orientation indicate a larger proportion meeting the good-outcome threshold in the endovascular arm; negative values indicate a smaller proportion. Zero represents no difference on this scale. Since the interval includes zero, the posted data do not exclude no difference at the interval’s confidence level.

How do the risk ratio and odds ratio differ?

In general, a risk ratio compares the proportions with an outcome in two groups by division. An odds ratio instead compares the odds of the outcome. Both express relative rather than absolute contrasts, and their numerical values do not mean the same thing as percentage-point differences. The registry reports a risk ratio of 1.75 with a confidence interval from 0.968 to 3.164, and an odds ratio of 4.0 with a confidence interval from 0.835 to 19.16. The null value for either ratio is 1. Both intervals include that value, and both are broad. When an outcome is not rare, odds ratios can also appear farther from the null than risk ratios; this is a general property of the measures, not a separate finding about the trial.

What does the p-value contribute?

The unadjusted p-value for the primary comparison is 0.074. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and analysis assumptions. It does not measure the probability that the null hypothesis is true, and it does not quantify the clinical importance of a result. The p-value should be considered alongside the estimated contrast and its confidence interval, not as a stand-alone verdict. The record does not report whether the posted comparison was adjusted for any covariates or other design features.

What is the role of randomization?

In general, random assignment aims to make treatment groups comparable in expectation, reducing systematic confounding in the comparison. It does not ensure that all characteristics will be balanced in a small trial. Nor does randomization by itself resolve issues such as missing outcome measurements, deviations from assigned treatment, or how participants are included in the analysis. The analysis population and handling of missing outcomes are not reported in the registry record.

Why does the distinction between raw mRS and mRS 0-2 matter?

The registry’s primary outcome entry presents a percentage achieving mRS 0-2, while the brief summary describes the primary objective in terms of raw mRS scores. In general, an analysis of the full ordered scale can use distinctions among all score levels, whereas a binary analysis treats all scores outside 0-2 as one category. These approaches answer related but not identical questions and can yield different estimates and inferential results. The specific raw-score analysis and its results are not reported in the registry record.

The trial is described as factorial, but the details needed to explain any factorial effects or interaction analyses are not reported in the registry record. No reported analyses are listed for the posted secondary outcomes. Thus, the available comparative interpretation rests on the estimates and unadjusted p-values recorded for the outcomes with numerical results, rather than a complete account of the trial’s statistical plan.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.321, with a 95% confidence interval from -0.002 to 0.645. In general, a confidence interval gives a range of estimates compatible with the observed data and the method’s assumptions. It is not a range containing a fixed proportion of individual participant outcomes, and it does not assign a probability to the true effect after the data have been observed. The interval’s lower end is close to zero and slightly below it, while the upper end is substantially larger. This leaves uncertainty about both whether the contrast is positive and how large it may be.

The relative measures are also imprecise. The risk ratio of 1.75 has a 95% confidence interval from 0.968 to 3.164. The odds ratio of 4.0 has a 95% confidence interval from 0.835 to 19.16. In general, the null value is 1 for ratios, and both intervals include that value. The broad ranges are consistent with the small group sizes and limited number of outcome events; a small number of participants can have substantial influence when the sample is small.

The sample sizes for the primary endpoint were 21 in the best medical therapy group and 12 in the endovascular treatment group. The unequal group sizes and small enrollment contribute to limited precision. The registry does not report confidence intervals for the arm-specific percentages themselves, but it does report intervals for the comparative measures.

Confidence intervals quantify statistical uncertainty under the assumptions used to calculate them. They do not account automatically for every limitation, such as possible selection effects, unreported analysis choices, or missing-outcome handling. Those details are not reported in the registry record. Precision should therefore be read from the posted intervals together with the trial’s limited enrollment and the specific population studied.

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 figures are illustrations based on the observed effect, not the trial’s original design justification. For these binary outcomes, the listed counts are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is a stated fraction of the observed effect. The trial’s own sample-size assumptions are not reported in the registry record.

For the primary good-outcome estimate, planning for 100% of the observed effect gives 36 participants per arm for 80% power and 48 participants per arm for 90% power. Planning for 75% of the observed effect gives 66 participants per arm for 80% power and 88 participants per arm for 90% power. Planning for 50% of the observed effect gives 151 participants per arm for 80% power and 202 participants per arm for 90% power.

In plain language, 80% power means that, under the planning assumptions and if the assumed effect were the true effect, a study of that size would have an 80% chance of detecting an effect at the stated significance level. The 90% column makes the corresponding chance 90%. These are design-planning concepts, not measures of what the completed trial achieved. The figures are not observed power.

Smaller effects require more participants to detect with the same power under the same assumptions. The illustration for 90-day mortality also uses the observed effect and lists 161 participants per arm for 80% power and 215 for 90% when planning for 100% of that effect; for 75%, the counts are 310 and 414; for 50%, they are 748 and 1,001. The original design assumptions and the reason for termination 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.429; treatment proportion p₁ = 0.750; average p̄ = 0.589.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6957 = 1.3636.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6576 = 0.5534.
4. n = (1.3636 + 0.5534)² / (0.3214)² = 35.6, rounded up to 36 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 <- 0.428571428571429                          # control proportion
p1 <- 0.75                          # 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(1852201)
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 = 36 (80% power), 48 (90% power)
 75% of observed effect: n per arm = 66 (80% power), 88 (90% power)
 50% of observed effect: n per arm = 151 (80% power), 202 (90% power)
power.prop.test: 35.6 
Simulated power at n = 36 per arm: 0.805 (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.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and eight posted secondary outcomes. The primary outcome is good functional outcome at 90 days, defined as mRS 0-2. Secondary outcomes include the 90-day mRS distribution, good functional recovery, mortality at 30 and 90 days, intracranial hemorrhage with neurological deterioration, procedure-related serious adverse events, arterial revascularization, and serious adverse events related to the thrombectomy device. Numerical results are available for only some of these outcomes in the registry record.

When several outcomes are tested, the chance of at least one apparently unusual result can increase if each is evaluated without accounting for the number of comparisons. In general, a prespecified multiplicity plan can define which outcomes are confirmatory, how the testing sequence works, or whether statistical thresholds are adjusted. A multiplicity strategy, outcome hierarchy, and any adjustment to secondary analyses are not reported in the registry record. The posted secondary p-values are unadjusted, so they should not be treated as independent confirmatory evidence.

The analysis population is not reported in the registry record. It is not stated whether participants were analyzed according to randomized assignment, treatment received, or another rule. The record also does not report the handling of missing outcome data, protocol deviations, crossovers, or withdrawals. These choices can affect both the denominator and the interpretation of randomized comparisons.

The primary outcome denominators are 21 for best medical therapy and 12 for endovascular treatment. The 30-day mortality outcome uses denominators of 17 and 12, respectively. The registry does not explain why the 30-day denominator differs from the primary outcome denominator, or how incomplete follow-up was handled. A difference in denominators is not by itself evidence of a particular missing-data mechanism.

The record describes the study as factorial but does not report the factors, planned contrasts, or analysis methods relevant to that structure. It also does not report the statistical analysis plan. These omissions prevent a complete assessment of the intended testing framework, the handling of missingness, and whether the posted estimates correspond to all prespecified analyses.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asymptomatic intracranial hemorrhage up to 24 hours post-randomization (33.3%), neurologic deterioration (14.3%), peripheal thromboembolic event (8.3%), worsening of pre existing condition-mid sternal chest pain (8.3%), l hip dislocation requiring closed reduction (8.3%).

The registry reports serious adverse events in 12 of 21 participants in the best medical therapy group and 4 of 12 participants in the endovascular treatment group. Other adverse events are reported for 10 of 21 participants and 9 of 12 participants, respectively. Death counts are 4 in the best medical therapy group and 1 in the endovascular treatment group. These are posted counts by group; the registry record does not provide a detailed account of event timing, seriousness criteria, or whether events overlapped within participants.

Among the listed serious adverse event terms, asymptomatic intracranial hemorrhage up to 24 hours post-randomization is reported as 33.3%, and neurologic deterioration as 14.3%. Other listed terms are reported as 8.3% each: peripheral thromboembolic event, worsening of pre-existing condition—mid sternal chest pain, left hip dislocation requiring closed reduction, and accidental narcotic overdose. These term percentages should be read as registry event listings, not as proof that treatment caused the events.

In general, small safety denominators make rates unstable, and adverse-event group counts alone do not establish comparative risk. The registry’s listed serious adverse events related to a thrombectomy procedure are a separate outcome, with numerical results reported for that outcome. The posted safety information does not establish whether any treatment caused or prevented an adverse event.

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

The central statistical finding is a higher observed percentage with mRS 0-2 at 90 days in the endovascular treatment arm than in the best medical therapy arm: 75.0% compared with 42.9%. The estimated risk difference is 0.321, but its 95% confidence interval, -0.002 to 0.645, includes zero and is broad. The unadjusted p-value is 0.074. These data describe an observed contrast and its uncertainty; they do not establish a precise effect size.

The result applies to the small randomized study population described in the registry: patients with acute ischemic stroke, ineligible for or refractory to IV-tPA, appropriately selected by imaging, and targeted for treatment within 6-12 hours. The record does not give enough detail about participants to extend the finding confidently to populations outside that description. It also does not report the reason the trial was terminated or the original sample-size rationale.

A non-significant or imprecise comparison does not show that two approaches are equivalent. Demonstrating equivalence or non-inferiority requires a design and analysis that specify an appropriate margin and test that question. Such a margin or analysis is not reported in the registry record. Likewise, the observed difference does not by itself show that the treatment caused the difference; interpretation depends on design execution, outcome completeness, and analysis choices that are not fully described in the registry record.

In general, statistical uncertainty and clinical importance are distinct. A confidence interval can be compatible with a range of effects, while clinical interpretation also depends on the relevance of the outcome and the study population. The registry does not report a threshold for a clinically important difference. Therefore, the posted estimates should be read as limited evidence from a small study, not as a definitive answer for all patients with stroke.

The record’s different descriptions of the primary endpoint also matter: the outcome entry is a percentage reaching mRS 0-2, while the brief summary refers to analysis of raw mRS scores. The specific analysis of the raw score distribution is not reported. This prevents assuming that the threshold-based comparison captures every aspect of the planned functional outcome analysis.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it pairs a clinically interpretable binary outcome with a small randomized sample. The observed group percentages differ, but the interval around the risk difference remains wide and includes zero. It illustrates why the point estimate alone is not enough: a seemingly substantial contrast can remain uncertain when the denominators are small.

It also highlights how outcome definition affects interpretation. The posted primary outcome uses a threshold of mRS 0-2, while the summary describes raw mRS scores and the overall distribution. A binary endpoint makes the proportion reaching a defined level easy to communicate, but in general it discards differences among scores within each category. Clear reporting of the intended estimand and analysis is especially important when a registry contains more than one description of the primary endpoint.

The registry’s factorial classification, with only two listed arms and no reported details about factors or interactions, illustrates another reporting challenge: a design label alone is not enough to reconstruct the planned comparison. Similarly, randomization is a valuable design feature, but an open-label trial with limited enrollment still requires careful interpretation of outcome assessment, missing data, and analysis populations. Those details are not reported in the registry record.

Finally, planning illustrations based on observed effects show how strongly required sample sizes depend on the effect one aims to detect. Smaller assumed effects require more participants under the stated planning assumptions. These figures are not the original design plan and do not describe the achieved power of the completed trial. Keeping planning calculations distinct from trial results helps prevent false precision or retrospective claims of power.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Enrollment was 33, with 21 participants in the best medical therapy arm and 12 in the endovascular treatment arm for the primary endpoint. The small and unequal group sizes limit precision and make estimates more sensitive to individual outcomes. The registry records a terminated status, but the reason for termination is not reported in the registry record; the effect, if any, of termination on enrollment or follow-up cannot be determined from the available information.

The population is narrowly framed around imaging-selected patients who were ineligible for or refractory to IV-tPA and treatment within 6-12 hours. Participant characteristics, site count, and details of imaging selection are not reported in the registry record. The findings therefore cannot be assumed to apply to patients outside the stated eligibility and timing description.

The registry classifies the model as factorial, but the factors and their analyses are not described. The primary endpoint is presented as a percentage meeting mRS 0-2, while the brief summary describes raw mRS analysis. The relationship between these descriptions and the actual analysis is not reported. Masking is listed as none; whether outcome assessors were masked is not stated.

The record does not report the analysis population, missing-data methods, protocol deviations, or the original sample-size justification. The 30-day mortality denominator is smaller in the best medical therapy group than the primary outcome denominator, but the reason is not given. Numerical results are not reported for all listed secondary outcomes. The statistical analysis plan and multiplicity approach are also not reported, which limits evaluation of how the results fit the intended testing strategy.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: POSITIVE Stroke Clinical Trial — NCT01852201.
• Registry record last updated 2019-11-13; status last verified 2019-11.
• Results first posted 2019-11-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The POSITIVE Stroke Clinical Trial was a randomized, unmasked study of endovascular treatment compared with best medical therapy for selected patients with acute ischemic stroke. Enrollment was 33, and the registry status is terminated. The primary outcome entry reports the percentage achieving mRS 0-2 at 90 days; the brief summary also describes raw mRS analysis.

The posted good-outcome percentages were 42.9% in the best medical therapy group and 75.0% in the endovascular treatment group. The risk-difference estimate was 0.321, with a 95% confidence interval from -0.002 to 0.645 and an unadjusted p-value of 0.074. The estimate is imprecise, and the record does not report the reason for termination, a complete analysis plan, or the handling of missing outcomes.