• Stroke

“If you are explaining, you’re losing” —Ronald Reagan

There remains a widespread conviction among most neurointerventionists and many non-interventional neurologists that mechanical thrombectomy is a life- and function-saving procedure in appropriately selected patients with acute ischemic stroke from large vessel occlusion (LVO). However, this has yet to be confirmed in a randomized controlled trial (RCT) for mechanical thrombectomy. While critical analyses of recent published RCTs provide insight into how they failed to demonstrate a benefit for thrombectomy, they do not negate their impact upon our field.1 Until we provide conclusive data in support of mechanical thrombectomy, our ability to offer this procedure to patients remains in constant jeopardy. In addition, as a larger volume of negative data accrues, our opportunities to conduct RCTs in this area will ultimately dissipate. For these reasons, now—more than ever—we must carefully and thoughtfully design future trials which will investigate, and potentially validate, the utility of endovascular stroke therapy in that patient population with the greatest potential for benefit.

Designing such a trial presents a challenge from the standpoint of equipoise, as many physicians believe it unethical to randomize a ‘likely to benefit’ patient to no treatment. However, given the negative data generated to date, it would be ill-conceived to dispense with equipoise for such patients. There are many past examples where treatment advocates were equally convinced of a lack of equipoise and subsequent RCTs demonstrated no benefit for intervention (eg, SAMPRIS, ECIC Bypass, COSS).2 ,3 In fact, one might posit that, in an appropriately designed RCT, it is better that the participating interventionists are believers in the benefits of the intervention and possibly have some reservations regarding procedural equipoise, but are still committed to the trial. Indeed, we believe firmly in the role of mechanical thrombectomy in appropriately selected patients while simultaneously arguing for an RCT. That properly designed RCT will then confirm our belief to be justified.

To design such a study, it is critical to learn from previous RCTs.1 ,4 In addition to providing evidence for equipoise, they also manifest rationales for caution with regard to trial design. In designing any future mechanical thrombectomy study, it is critical we have a pragmatic outlook. To this end we highlight a number of key considerations for such a pragmatic study design.

1. Appropriate power: We must avoid overestimating effect size. The literature is replete with procedural and drug trials that failed, or were never completed, due to gross overestimates of effect size. We should use the highest quality evidence-based data available to generate conservative estimates. Rather than allowing our hopes to cloud our expectations, we should seek to establish confirmation of a reasonable clinically significant benefit. Overestimation of effect size leads to an inadequate sample size and reduces the probability of demonstrating any significant benefit for intervention (statistical type II error). There is every reason to be pragmatic and conservative with respect to our effect size estimates (and subsequent sample size). It is far better to incorporate an interim data analysis with early stopping rules (with appropriate statistical methodology) than to conclude study enrollment to reveal a non-significant beneficial trend, which ultimately leads to an erroneously negative primary conclusion.

2. Randomize patients we think have the most potential to be helped by mechanical thrombectomy:

   1. Patients who are ineligible for intravenous tissue plasminogen activator (IV tPA) or who have failed IV tPA: Control data from Prolyse in Acute Cerebral Thromboembolism II (PROACT II) and Mechanical Retrieval and Recanalization of Stroke Clots Using Embolectomy (MR RESCUE) trials provide insight into the prognosis for patients with large vessel occlusion who do not receive either IV lytic or intra-articular endovascular therapy. In PROACT II and MR RESCUE, these patients had only a 25% and 23% rate of favorable outcome at 90 days, respectively. It is thus fair to say that these patients have a dismal prognosis with medical management and theoretically should have the greatest potential to be helped by interventional therapies. In contrast, in the Interventional Management of Stroke III (IMS III) trial, comparable control patients who received IV tPA had considerably better outcomes at 90 days (39%). Better outcomes in the medical management arm places significantly more pressure on the effect size required to demonstrate a benefit for thrombectomy. Furthermore, the within-group variability for a typical IV tPA LVO cohort is greater given the subset of patients who recanalize from IV tPA. This widened variability further limits a study's ability to demonstrate a statistical difference between cohorts. For this reason, a comparison against a control arm of standard medical therapy and IV tPA-resistant patients is most attractive and, in our opinion, most appropriate.

   2. Patients presenting at early time points: Pooled data from the IV tPA trials, as well as data from IMS III, have consistently indicated that time from symptom onset to revascularization is a critical determinant of patient outcome.5 PROACT II, and to some extent the Middle Cerebral Artery Embolism Local Fibrinolytic Intervention Trial (MELT), provide data that support the benefit of interventional therapies up to 6 h after presentation.6 ,7 If the Merci arms of the Solitaire With the Intention For Thrombectomy (SWIFT) trial and the Thrombectomy REvascularization of large Vessel Occlusions in acute ischemic stroke (TREVO) trial are considered a ‘surrogate’ for medical therapy, there is reason to believe that a clinically significant beneficial effect of interventional therapy with modern thrombectomy devices could be realized up to 8 h.8 ,9 After 8 h there are no high-quality prospective trial data that support intervention. As such, extending the window beyond 8 h poses some risk. While there are many data that suggest a potential for advanced patient selection paradigms to be of value, at present these data are not definitive. As a result, we should be cautious in the inclusion of patients with delayed presentation. The most definitive evidence for the benefit of recanalization-based therapy is in the 0–4.5 h window. Therefore, this population probably provides the best opportunity to demonstrate the benefit of thrombectomy. Alternatively, trials that include patients at later treatment times must exert great care in the design of the trial to account for the inclusion of delayed patients, such as stratification according to time of presentation and statistically valid prespecified subgroup analyses.

   3. Patients with small core infarcts (<50 mL): Core infarct volume imaging—be it based on the Alberta Stroke Program Early CT Score (ASPECTS), MRI or CT—represents an accurate predictor of outcome after thrombectomy.10 Fewer than 8% of patients with core infarcts >50 mL achieve good functional recoveries by 90 days compared with 55% with core infarcts <50 mL. As such, including patients with large core infarcts at presentation will substantially reduce the effect size for thrombectomy and increase the variability within the cohort. Once again, these changes reduce the chances of observing a benefit for the therapy. Imaging selection to avoid those patients with large cores of established infarction must be enacted in any potentially successful trial.

3. Primary outcomes should be compared across all Rankin values (ie, a Rankin shift analysis rather than as a binary (0–2 vs 2–6) analysis:) A number of factors can make it exceedingly unlikely that a stroke patient will achieve an excellent functional outcome (modified Rankin Scale (mRS) score <2) at 90 days. First, the emergency assessment of the premorbid function of patients in the setting of acute ischemic stroke can be difficult. As such, in any stroke trial there is a risk of inadvertently including patients with mRS score >1 prior to their stroke onset. These types of patients are exceedingly unlikely to achieve an excellent outcome regardless of the efficiency of the thrombectomy. Second, elderly patients may be less likely to make an excellent functional recovery even after an efficient thrombectomy, particularly if they have additional non-neurological comorbidities which may impair their recovery. Third, patients at later time points (>6 h) and with an initially severe stroke at presentation may have larger baseline core infarct volumes or involvement of more eloquent areas, again limiting their ability to return to near normal neurological function. While each of these patient cohorts might improve substantially with effective thrombectomy, this improvement might be from an mRS score of 5–6 to 3 rather than to ≤2. While this type of procedural success and improved outcome between cohorts is reflected with a shift analysis, it is broadly categorized as a failure with a binary endpoint analysis.

   Moreover, it is challenging to predict the ‘cluster of benefit’ which will be observed after thrombectomy in a given patient population a priori.11 For instance in the MELT study, due to the inclusion of earlier patients with smaller core infarcts and less severe strokes than in PROACT II trial, the benefit cluster occurred at mRS ≤1 rather than mRS ≤2.7 As such, despite a clear beneficial effect across all Rankin categories and a beneficial effect using a binary endpoint of mRS ≤1, the study failed on its prespecified primary outcome (mRS ≤2) due to this incorrect prediction of the ‘cluster of benefit’. The same phenomenon is seen in the SWIFT trial data, which fails on a binary mRS score of ≤2 endpoint to demonstrate a clinical beneficial effect of Solitaire over MERCI, while overwhelmingly superior when analyzed as a shift.8 As a community we shackle ourselves by choosing a scale of already limited sensitivity, the mRS, and then further reduce its statistical sensitivity by dichotomizing it. Such an outcome reduces power, creates an artificial threshold of success and is highly statistically insensitive. For instance, the dichotomized mRS score of <2 also ignores the possible effect of thrombectomy converting large numbers of patients with an mRS score of 3 to an mRS score of 6 due to procedural complications. In either direction (pro or con), dichotomization is insensitive. Lastly, it presupposes that an mRS score of 3 is not a good outcome. However, in our experience of clinical discussions with patients and their families, most patients with a high NIH Stroke Scale score would consider an mRS score of 3 as an acceptable outcome whereas almost none would accept an mRS score of 4. We do not mean to suggest that we should instead dichotomize at a new threshold, but rather that the very act of dichotomization creates a false impression that there is some binary definition of good versus poor outcome. Rather, the effectiveness of a therapy should be evaluated over the entire range of outcome scores.

4. Active real-time monitoring of operators within the study: During the course of a study the enrollment of inappropriate patients can blunt the effect of the intervention. Within the context of a stroke trial, this would include enrollment of patients with large core infarct volumes at presentation. As such, in a trial it is important to actively and contemporaneously monitor the performance of sites with respect to patient selection. An imaging core laboratory should be available to promptly evaluate imaging submitted for enrolled patients so that any errors in interpretation can be quickly identified. Equally important is an independent system of active monitoring of proceduralists’ performance. Sites with high rates of procedural complications, unusual procedural complications or poor revascularization rates must be identified as efficiently as possible. Sites/investigators who are outliers with respect to these types of performance metrics must be counseled and, if need be, placed on enrollment hold.

5. Sufficient enrollment rate to achieve completion within a relevant time period: We must consider all possible means of optimizing enrollment. A waiver of consent represents an important potential mechanism by which to achieve this. Challenges to obtaining consent for such a time-dependent emergency procedure can be significant, particularly as many patients are transferred to the center providing the thrombectomy. The family are often still en route as the patient gets evaluated, and Institutional Review Boards will not accept telephone consents for trials. It would be extremely helpful to petition for a waiver of consent for an acute ischemic stroke study, and there is some precedent from other disciplines to suggest that this is possible. This mechanism could markedly improve the efficiency of patient enrollment at participating sites and reduce the time to treatment for patients enrolled. Precedents for enrolling patients under consent waivers exist in the trauma literature where parallel circumstances are encountered.1,2 Second, it is important that our field actively undertakes this type of definitive trial as a unified effort. Concurrent protocols slow the completion of a single decisive successful study and may negatively impact such an effort by competing for patient enrollment. At minimum, when parallel processes are in place, such trials should come to a prespecified agreement to pool data for combined prespecified analyses after trial completion.