A Randomized, Concurrent Controlled Trial to Assess the Safety and Effectiveness of the Separator 3D as a Component of the Penumbra System in the Revascularization of Large Vessel Occlusion in Acute Ischemic Stroke: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Randomized, Concurrent Controlled Trial to Assess the Safety and Effectiveness of the Separator 3D as a Component of the Penumbra System in the Revascularization of Large Vessel Occlusion in Acute Ischemic Stroke (NCT01584609), a randomized na study. The primary outcome is Number of Participants With Angiographic Revascularization of the Occluded Target Vessel.

2. Clinical Question

The comparison is between two device strategies, not between a device and no intervention. Both groups received the Penumbra System; the distinguishing component was whether Separator 3D was used. This matters when interpreting the contrast: the result describes the incremental comparison of the system with Separator 3D against the system alone in the enrolled trial population.

The primary endpoint is a count of participants meeting a post-procedure angiographic definition. It is not a direct measure of later functional status, quality of life, or survival. The record also lists secondary outcomes involving clinical outcome, disability status, mortality, symptomatic intracranial hemorrhage, and neurological outcome. Those outcomes address different aspects of participants’ subsequent clinical course and should not be treated as interchangeable with immediate angiographic revascularization.

3. Trial Design

The registry record describes a prospective, randomized, single-blind, concurrent-controlled, multicenter study with a parallel-group model. Participants were assigned to the Penumbra System with Separator 3D or the Penumbra System alone. The record identifies the study as completed and lists enrollment as 198. The brief summary describes a plan for up to 230 evaluable participants at up to 50 centers; the registry record does not explain the relationship between that planned figure and the enrollment figure.

The population described in the brief summary had symptoms of acute ischemic stroke and evidence of a large-vessel occlusion in the cerebral circulation. The vessel was described as 2.5mm or greater in diameter and accessible to the Penumbra Separator 3D System. Revascularization was to occur within 8 hours of symptom onset. These are summary-level eligibility details; additional inclusion and exclusion criteria are not reported in the registry record.

The study began in 2012-04, and primary completion is listed as 2017-06. Each treated patient was to be followed and assessed for 3 months after randomization. The primary endpoint was assessed at immediate post-procedure, while secondary outcomes include timeframes at 30 days and 90 days. The record labels masking as single but does not report which participants or study personnel were masked. It lists the phase as NA.

Random allocation and concurrent groups support a comparative design, but the registry record does not give details of the randomization sequence, concealment, stratification, or center-level procedures. It also does not report the original sample-size justification or a detailed protocol for handling deviations from assigned treatment. Those details should not be inferred from the enrollment count or from the posted comparisons.

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

Analysis population for the primary outcome, as defined in the registry: Analysis population demonstrate outcomes of number of subjects that met endpoint.

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 Number of Participants With Angiographic Revascularization of the Occluded Target Vessel, measured over At immediate post-procedure.

The primary endpoint counts participants with angiographic revascularization of the occluded target vessel. The registry definition is mTICI grade 2-3, assessed at immediate post-procedure. In plain terms, this is an imaging-based, procedure-proximal measure of whether the target vessel met the stated revascularization threshold. It is recorded as a participant count rather than as a continuous measurement.

This type of endpoint is used to quantify a specific technical or anatomical result of the procedure. It gives a direct comparison of how many participants in each assigned group met the prespecified registry definition. It is distinct from a later clinical outcome: meeting the angiographic threshold does not itself summarize subsequent disability, neurological status, mortality, or adverse events. Those topics are represented by separate secondary outcomes in the record.

The primary endpoint is relevant to the trial’s stated question because the study compares two versions of the Penumbra System for revascularization. The summary says the hypothesis was that the system with Separator 3D would be non-inferior to the system alone for revascularization of large-vessel occlusion. However, the endpoint results alone do not establish a formal non-inferiority conclusion. The non-inferiority margin, the planned analysis method, and a reported inferential analysis against that margin are not reported in the registry record.

For the primary comparison, 82 of 94 participants in the Separator 3D group and 79 of 96 in the system-alone group met the endpoint. The posted risk difference is expressed as system alone minus system with Separator 3D. Its estimate and confidence interval describe the size and uncertainty of that contrast, rather than a separate clinical outcome.

7. Results Posted in the Registry

• Penumbra System Alone: 82.3% (79/96) versus 87.2% (82/94) on control; risk difference -4.9 percentage points (95% CI -15.1 to 5.2), risk ratio 0.94 (0.84–1.06); unadjusted two-proportion z-test p = 0.344.

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.

Good Clinical Outcome at 30 Days

• 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:
  • Penumbra System Alone: 55.0% (55/100) versus 59.8% (58/97) on control; risk difference -4.8 percentage points (95% CI -18.6 to 9.0), risk ratio 0.92 (0.72–1.17); unadjusted two-proportion z-test p = 0.496.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Penumbra System Alone and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With 90 Day mRS Score 0-2

• 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:
  • Penumbra System Alone: 45.8% (44/96) versus 45.3% (39/86) on control; risk difference 0.5 percentage points (95% CI -14.0 to 15.0), risk ratio 1.01 (0.74–1.39); unadjusted two-proportion z-test p = 0.948.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Penumbra System Alone and the control. The interval gives the range of effects that remain compatible with the data.

All Cause Mortality

• 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:
  • Penumbra System Alone: 26.0% (26/100) versus 19.4% (19/98) on control; risk difference 6.6 percentage points (95% CI -5.0 to 18.2), risk ratio 1.34 (0.80–2.26); unadjusted two-proportion z-test p = 0.267.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Penumbra System Alone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address several different dimensions and timepoints: good clinical outcome at 30 days, mRS score 0-2 at 90 days, all-cause mortality, symptomatic intracranial hemorrhage, and good neurological outcome at 90 days. The posted quantitative comparisons in the registry record cover three of these outcomes; the remaining secondary outcomes are not accompanied by arm comparisons in the listed results. The available secondary estimates do not all point in the same direction, and their intervals show substantial uncertainty.

This mixed pattern does not contradict the primary endpoint, because the outcomes are not measuring the same event. The primary result concerns immediate angiographic revascularization, while the secondary outcomes concern later clinical status or mortality. A difference in a procedure-proximal measure need not map directly onto a later outcome, and a later outcome is affected by more than the angiographic endpoint alone. The registry record does not provide analyses linking individual participants’ primary and secondary outcomes.

Secondary outcomes can help describe whether the overall clinical pattern is consistent across different domains, but they should not be combined into a single conclusion without a prespecified method. The available data do not establish a consistent advantage across outcomes. Nor should variation in the directions of the estimates be treated as proof of true differences between endpoints; sampling uncertainty is considerable in these comparisons.

Unadjusted secondary results carry less weight because multiple outcomes create multiple opportunities for apparently notable findings. The registry record does not report a multiplicity adjustment, an outcome hierarchy, or a plan that identifies particular secondary outcomes as confirmatory. The secondary findings are therefore best read as supportive descriptive evidence rather than as independent proof of a treatment effect. Their interpretation should also take account of the varying denominators and the absence of reported missing-data and analysis-population details.

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

• Good Clinical Outcome at 30 Days
• Number of Participants With 90 Day mRS Score 0-2
• All Cause Mortality
• Number of Symptomatic Intracranial Hemorrhage
• Good Neurological Outcome at 90 Days

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the angiographic revascularization definition or did not. The registry reports the number meeting the endpoint and the number in each group. A risk, in this context, is the proportion of participants who meet the binary outcome. The comparison is summarized as a risk difference, which subtracts the risk in one group from the risk in the other. Here, the stated contrast is system alone minus system with Separator 3D, so a negative estimate indicates a lower observed endpoint proportion in the system-alone group.

A risk difference is an absolute contrast. It is expressed on the probability scale and answers how far apart the observed group proportions are. It differs from a risk ratio, which expresses a relative contrast, and an odds ratio, which compares odds rather than risks. These measures can tell different stories about the scale of an effect, particularly when the outcome is not rare. They do not change the underlying observed counts. The registry record also includes relative measures for the primary comparison, but the central interpretation can be made from the risk difference and its interval.

A confidence interval describes the uncertainty around an estimate under the statistical method used to construct it. It gives a range of values reasonably compatible with the observed data and the method’s assumptions. It is not a guarantee that the true effect lies in the interval, and it is not a probability statement about the particular effect. For this primary result, the interval includes zero, which corresponds to no absolute difference on the risk-difference scale. The width of the interval also matters: a range extending meaningfully in both directions leaves substantial uncertainty about the size and direction of the contrast.

The unadjusted p-value is a test statistic translated into a probability under a null model and the test assumptions. It does not measure the size or clinical importance of a difference. It is not the probability that the null is true, and it does not establish that two strategies are equivalent when it is not small. A p-value should be read with the estimate, its interval, the study question, and the analysis plan. In this trial, the stated question is non-inferiority, which is not answered by a conventional test for any difference alone.

Non-inferiority testing asks whether the intervention is not unacceptably worse than a comparator by more than a prespecified margin. The margin defines the largest loss that would still satisfy the criterion. The confidence interval is then assessed relative to that margin, with attention to the direction in which worse outcomes are defined. The margin, the formal non-inferiority analysis, and the original analysis plan are not reported in the registry record. It is therefore not possible to reconstruct that test from the posted risk difference and unadjusted p-value.

Randomization is intended to make the assigned groups comparable, on average, with respect to measured and unmeasured characteristics. It does not guarantee perfect balance in a particular trial, especially when the group sizes are finite. A concurrent comparator helps distinguish the intervention contrast from changes over time that affect both groups. The registry record identifies random allocation and a concurrent-controlled parallel design but does not report the sequence-generation or allocation-concealment methods. Those implementation details cannot be assessed from the listed design labels.

Counts and denominators vary across the primary and secondary outcomes. For example, the primary endpoint uses 94 and 96 participants as group denominators, whereas some secondary outcomes use different denominators. Such variation can arise for multiple reasons, but the reason for each denominator is not reported in the registry record. A denominator should therefore be read as the analysis set for that particular posted outcome, not assumed to represent every randomized participant.

Binary-outcome comparisons also depend on how missing outcomes are treated and on which participants are included. An intention-to-treat analysis generally compares participants according to randomized assignment, while a per-protocol analysis restricts the comparison according to adherence or protocol criteria. These approaches can matter in non-inferiority studies because departures from assigned treatment and missing data may affect the estimated contrast. The registry record does not identify the primary analysis population or describe missing-data handling, so neither approach should be presumed.

Multiplicity arises when several outcomes or comparisons are examined. Testing many outcomes can increase the chance of obtaining an apparently notable result by chance if no adjustment or hierarchy is used. The record lists several secondary outcomes, but does not report a multiplicity strategy, a hierarchy among outcomes, or adjusted secondary analyses. Secondary findings should consequently be treated as exploratory unless a prespecified analysis plan establishes otherwise. The posted secondary comparisons are unadjusted, and their p-values should not be interpreted as if they were the only tests undertaken.

Finally, the registry record reports no analysis entries. This means the record does not describe methods such as covariate adjustment, stratification in the analysis, center effects, or sensitivity analyses. It does not mean that no such work occurred; it means those details are not reported in the registry record. The posted summary statistics can be described directly, while claims about unreported analytic choices remain unwarranted.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.049 for system alone minus system with Separator 3D. Its 95% confidence interval runs from -0.151 to 0.052. The lower and upper bounds are on opposite sides of zero, so the interval includes no absolute difference and also allows differences in either direction. This is why the point estimate alone is not enough to characterize the comparison.

Precision refers to how tightly the data locate an effect estimate. A narrower confidence interval would indicate more precision under the same method; a wider interval leaves more plausible values. The primary interval spans a meaningful range around the estimate, so the observed contrast is not estimated with high precision. The posted data do not identify one exact difference as the only credible interpretation.

The confidence interval does not say that there is a 95% probability that the true effect lies between its bounds. It describes the behavior of the interval-generating procedure over repeated samples under its assumptions. For an individual trial, it is best used as a range of effect sizes reasonably compatible with the observed data, while remembering that the interval depends on the method and analysis population.

For this study, uncertainty has a particular implication because the stated hypothesis is non-inferiority. The relevant question would be whether the confidence interval rules out an unacceptable loss defined by a prespecified margin. That margin is not reported in the registry record. Consequently, the interval can be described as including zero and extending in both directions, but it cannot be used to verify the stated non-inferiority criterion without the missing margin and formal 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 planning figures are participants per arm, not total participants, for the binary outcomes listed. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record; these calculations are planning illustrations based on the observed results, not a reconstruction of the trial design.

The 80% power column gives the number of participants per arm estimated to yield an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the calculation assumptions were correct. The 90% power column expresses the corresponding target for a 90% chance. These are prospective planning quantities: they describe what a hypothetical study might need, not the probability that the completed trial detected an effect. This is not observed power.

Rows that plan for 100%, 75%, or 50% of the observed effect vary the effect size being targeted. A smaller effect is harder to distinguish from random variation, so detecting it at the same target power generally requires more participants per arm. The figures can rise sharply when the observed contrast is small, as is especially apparent for the 90-day mRS endpoint. Such large planning values should be read as a consequence of the selected effect and assumptions, not as evidence that the original study was designed for that number of participants.

The sample-size curve is another way to view the relationship between a planning target and the required number of participants. It should be interpreted as an illustration conditional on the stated calculation assumptions. It does not account for unknown details of the original protocol, possible missing outcomes, a non-inferiority margin, multiplicity, or a revised estimate from an independent study. The planning exercise uses observed effects, which are themselves uncertain and may be unstable in a modest-sized study.

These calculations do not establish whether the completed trial was adequately powered for its stated non-inferiority question. That judgment would require the original design assumptions, including the non-inferiority margin and planned analysis, which 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 = 0.872; treatment proportion p₁ = 0.823; average p̄ = 0.848.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5082 = 0.9961.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5070 = 0.4267.
4. n = (0.9961 + 0.4267)² / (-0.0494)² = 828.8, rounded up to 829 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 <- 0.872340425531915                          # control proportion
p1 <- 0.822916666666667                          # 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(1584609)
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 = 829 (80% power), 1,110 (90% power)
 75% of observed effect: n per arm = 1,425 (80% power), 1,907 (90% power)
 50% of observed effect: n per arm = 3,095 (80% power), 4,142 (90% power)
power.prop.test: 828.8 
Simulated power at n = 829 per arm: 0.801 (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 record lists multiple secondary outcomes in addition to the primary angiographic endpoint. When several outcomes are examined, the chance of seeing an apparently unusual result by chance can increase. A prespecified outcome hierarchy or multiplicity adjustment can help control that issue, but such a strategy is not reported in the registry record. The available secondary comparisons are unadjusted, and no reported analyses describe how their interpretation was handled as a group.

The registry record gives no analysis entries. It does not report whether outcomes were analyzed according to intention to treat, per protocol, or another defined population. It also does not describe how participants with unavailable endpoint data were handled, whether imputation was used, or whether sensitivity analyses examined alternative assumptions about missing outcomes. These omissions matter because the primary endpoint denominators and secondary endpoint denominators differ, and the reasons are not stated.

For a non-inferiority study, analysis population and missing-data decisions can be especially consequential. Different analysis populations may yield different estimates, and missing outcomes can make a comparison appear more favorable or less favorable depending on the assumptions used. This is a general statistical concern, not evidence that any particular bias occurred in this trial. Without the analysis plan and reporting of missingness, the robustness of the posted comparison to these choices cannot be assessed.

The record also does not report the non-inferiority margin or a formal non-inferiority test. It is not possible to evaluate whether the analysis followed a prespecified margin, whether the primary result met the criterion, or how any deviations from the planned approach were handled. The protocol’s sample-size justification, interim analysis plans, and detailed statistical methods are not reported in the registry record.

These gaps limit interpretation of the posted p-values and confidence intervals, but they do not erase the descriptive information in the counts and estimates. The most defensible reading is to report those results as posted while keeping the unreported analysis choices, missing-data handling, multiplicity strategy, and non-inferiority criteria as unresolved features of the evidence.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: nervous system disorders (30.1%), respiratory, thoracic, and mediastinal disorders (11.8%), cardiac disorders (11.4%), gastrointestinal disorders (10.8%), vascular disorders (9.7%).

The adverse-event figures use denominators that differ from the primary endpoint groups. In the Separator 3D group, 38 of 88 participants at risk were affected by a serious adverse event; in the system-alone group, 49 of 93 were affected. Other adverse events affected 81 of 88 and 83 of 93 participants, respectively. The record lists 19 deaths in the Separator 3D group and 26 in the system-alone group. These are posted counts and denominators; they should not be assumed to use the same analysis population as the primary endpoint.

The registry also lists serious adverse-event categories, including nervous system disorders at 30.1%, respiratory, thoracic, and mediastinal disorders at 11.8%, and cardiac disorders at 11.4%. Other listed categories are gastrointestinal disorders at 10.8%, vascular disorders at 9.7%, and infections and infestations at 6.5%. These category percentages describe the registry’s listing and should not be interpreted as comparative risks between the randomized groups without corresponding group-specific data and denominators.

Counts alone do not establish whether an event was caused by a device or procedure. The record does not provide event-level timing, severity details, adjudication procedures, or a comparative statistical analysis of these safety outcomes. These figures describe reported events and should be interpreted with those limitations in mind.

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

The primary result describes the number of participants in each assigned group who met the registry’s immediate angiographic definition. The posted estimate is a modest negative risk difference for system alone relative to system with Separator 3D, but the confidence interval includes zero and spans differences in both directions. The data therefore do not precisely locate the group contrast.

This result does not show that the two device strategies are equivalent. A failure to demonstrate a conventional statistically significant difference is not the same as demonstrating equivalence. Equivalence requires its own prespecified margins and an analysis designed to determine whether the full range of plausible differences lies within those margins. Those margins and a formal equivalence analysis are not reported in the registry record.

Nor does the primary comparison by itself establish non-inferiority. The trial summary states a non-inferiority hypothesis, but the record does not report the margin or a formal analysis against it. A confidence interval that includes zero is not enough to decide that question. The result should be described as an observed estimate with its uncertainty, rather than as a definitive confirmation or rejection of the stated hypothesis.

The endpoint is angiographic and assessed immediately after the procedure. It should not be interpreted as a direct estimate of later clinical outcome, neurological status, disability, or survival. The registry lists these as separate outcomes, with distinct timeframes and denominators. They provide additional information about different aspects of the trial but do not transform the primary endpoint into a patient-centered measure.

The record also does not report enough detail to determine whether results are robust to missing-data assumptions, analysis population choices, or multiplicity. These limits do not mean that the posted data are invalid; they describe boundaries on what can be concluded from the registry record. The evidence supports a careful account of the observed counts and uncertainty, not a treatment recommendation or a broad claim beyond the studied comparison and population.

17. Why This Trial Matters Statistically

This trial illustrates why a non-inferiority question needs more than a point estimate and a conventional test for difference. A non-inferiority conclusion depends on a prespecified margin, a suitable confidence interval, and an analysis plan aligned with the hypothesis. The registry record states the hypothesis but does not report the margin or formal test. That gap is central to interpretation, rather than a minor reporting detail.

The study also illustrates the distinction between a proximal procedural endpoint and later clinical outcomes. Angiographic revascularization is a specific endpoint with a clear registry definition, while later outcomes describe other dimensions of participants’ status. Different measures can produce estimates in different directions without being logically inconsistent. Statistical interpretation should preserve those distinctions rather than collapse all outcomes into a single verdict.

Finally, the record demonstrates how counts, effect estimates, confidence intervals, and p-values each contribute different information. Counts show the observed endpoint events; the risk difference gives an absolute contrast; the confidence interval conveys uncertainty; and the p-value summarizes compatibility with a specified null model. None of these pieces alone answers every question about clinical importance, precision, or non-inferiority. Reading them together—and recognizing what the record does not report—supports a more restrained and transparent interpretation.

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.

The main limitation for interpreting the primary result is that the stated non-inferiority hypothesis cannot be evaluated fully from the registry record: the margin and formal analysis are not reported. The record also omits the trial’s original sample-size justification and detailed statistical analysis plan. Planning illustrations based on the observed effect do not replace those design details.

Some design and analysis information is incomplete. Although masking is listed as single, the masked party is not identified. The record does not describe randomization sequence generation, allocation concealment, prespecified analysis populations, or the handling of missing outcomes. It also does not report the reasons that participant denominators differ across endpoints. These omissions limit assessment of potential bias and robustness, without demonstrating that bias occurred.

The secondary results are subject to uncertainty and are unadjusted in the posted comparisons. The registry does not report a multiplicity strategy or a hierarchy for interpreting secondary outcomes. In addition, quantitative comparisons are not listed for every secondary outcome named in the record. This limits the extent to which the secondary findings can be combined into a comprehensive account of clinical outcomes.

Safety counts are reported with their own at-risk denominators, but the record does not provide event-level detail, comparative tests, or enough information to attribute events to a device or procedure. Finally, the posted results come from the recorded trial population and endpoint definitions; generalization beyond those conditions is not established by the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Randomized, Concurrent Controlled Trial to Assess the Safety and Effectiveness of the Separator 3D as a Component of the Penumbra System in the Revascularization of Large Vessel Occlusion in Acute Ischemic Stroke — NCT01584609.
• Registry record last updated 2018-09-13; status last verified 2018-08.
• Results first posted 2018-09-13.
• 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

NCT01584609 is a completed, randomized, single-blind, parallel-group, concurrent-controlled trial sponsored by Penumbra Inc. It compared the Penumbra System with Separator 3D against the Penumbra System alone in patients described as having acute ischemic stroke from large-vessel occlusion. Enrollment is listed as 198.

The primary endpoint was the number of participants with angiographic revascularization of the occluded target vessel, defined as mTICI grade 2-3 at immediate post-procedure. The posted risk difference for system alone minus system with Separator 3D is -0.049, with a 95% confidence interval from -0.151 to 0.052 and an unadjusted p-value of 0.344.

The trial summary states a non-inferiority hypothesis. The non-inferiority margin, original sample-size justification, analysis populations, missing-data methods, and multiplicity strategy are not reported in the registry record. Accordingly, the posted results describe the observed comparison and its uncertainty but do not establish a formal non-inferiority conclusion.