Source: Twelve high-quality trials have been completed, see list below
Efficacy Endpoints: Mortality, neurologic improvement
Harm Endpoints: Intracranial hemorrhage, mortality
Narrative: Thrombolysis has been rigorously studied in >60,000 patients for acute thrombotic myocardial infarction, and is proven to reduce mortality. It is theorized that thrombolysis may similarly benefit ischemic stroke patients, though a much smaller number (8120) has been studied in high quality trials thus far.
There are 12 such trials 1-12. Despite the temptation to pool these data the studies are clinically heterogeneous. While statistical heterogeneity refers to variation in the results of different trials, and is quantifiable using p- and I2 values, clinical heterogeneity refers to variations in study design, setting, and population characteristics.* Data from multiple trials must be clinically and statistically homogenous to be validly pooled.14 Large thrombolytic studies demonstrate wide variations in anatomic stroke regions, small- versus large-vessel occlusion, clinical severity, age, vital sign parameters, stroke scale scores, and times of administration. Even within a prominent and recent meta-analysis examining a single agent this continues to be true, as supported by clear statistical heterogeneity in the most important outcomes of such trials (see Table 2).15
Examining each study individually is therefore, in our opinion, both more valid and more instructive. The reference list below includes information from each study including size, primary outcomes, results, and times to treatment. Studies in green conclude a benefit. Those in blue conclude no benefit. Those in red were stopped early due to harm.
Two of twelve studies suggest a benefit, NINDS-2 and ECASS-3. Unfortunately both use nonstandard data analysis and reporting, and there is a lack of clarity in both. To wit, the ‘NINDS’ publication is two studies. The first (NINDS-1) tested neurologic improvement at 24 hours and found no benefit. NINDS-2 then sought “a difference of 20 percentage points" at 90 days between groups, and it is unclear whether this meant a difference between groups in degree of improvement (i.e. the outcome in NINDS-1) or in 'the chance of a good outcome’. The paper reported only the latter. This is unfortunate because subjects in the thrombolytic arm experienced milder strokes than those in the placebo arm. Patients with milder strokes are obviously more likely to achieve a ‘good outcome’, making degree of improvement a much better comparison.
Ultimately NINDS-2 reported that 12% more subjects experienced ‘good’ outcomes in the thrombolytic group. Despite being not close to the 20% goal this is reported as a statistically significant difference. The choice not to analyze the data as they had in the first study remains unexplained and non-intuitive.
The second study suggesting benefit is ECASS-3, which again exhibited severity imbalances that favored the thrombolytic arm, and again dichotomized outcomes as good/bad. Moreover, a mathematical error of p-value calculations in ECASS-3 calls into question the published result.16
Regardless of the irregularities in these two industry-funded investigations, they remain the only two claiming benefit. In comparison, twice as many studies showed harm and these were stopped early. This early stoppage means that the number of subjects in studies demonstrating harm would have included over 2400 subjects based on originally intended enrollments. Pooled analyses are therefore missing these phantom data, which would have further eroded any aggregate benefits. In their absence, any pooled analysis is biased toward benefit. Despite this, there remain five times as many trials showing harm or no benefit (n=10) as those concluding benefit (n=2), and 6675 subjects in trials demonstrating no benefit compared to 1445 subjects in trials concluding benefit.
Finally, the issue of time windows remains open as an important confounding variable. Are thrombolytic agents, for instance, beneficial in the setting of the first 3h from onset? This argument would be the strongest time window argument to make based on NINDS-2 and subgroup results from IST-3. However, presuming that early (0-3h) administration is better than later administration (3-4.5h or 4.5-6h) the subgroup results of IST-3 suggest an implausible biological effect in which early administration is beneficial, 3-4.5h administration is harmful, and 4.5-6h administration is again beneficial. Incidentally, each of these subgroups in IST-3 represents a larger 'n' than any existing single trial of thrombolytics prior to IST-3, making the comparison extremely powerful. Based on these time window effects the p-value calculation testing for the hypothesis that time to administration was a significant predictor of effect in IST-3 was 0.61 (see figure 3 in the original publication). This essentially removes time as an important variable, an argument first proposed by the Cochrane Collaboration review based on their mathematical calculations of data generated prior to IST-3.17
Thrombolytics for ischemic stroke may be harmful or beneficial. The answer remains elusive. We struggled therefore, debating between a 'yellow' or 'red' light for our recommendation. However, over 60,000 subjects in trials of thrombolytics for coronary thrombosis suggest a consistent beneficial effect across groups and subgroups, with no studies suggesting harm. This consistency was found despite a very small mortality benefit (2.5%), and a very narrow therapeutic window (1% major bleeding). In comparison, the variation in trial results of thrombolytics for stroke and the daunting but consistent adverse effect rate caused by ICH suggested to us that thrombolytics are dangerous unless further study exonerates their use.
* There are ongoing debates about how much clinical heterogeneity is too much, but there are extremes of agreement. It would be possible to combine, for instance, prayer and surgery into a review of 'The Effectiveness of Therapy for Back Pain'. The two will have about the same effect at 6 months and therefore will be 'statistically homogeneous'. But the two therapies are physiologically and mechanically different, and should not be pooled. Thus low statistical heterogeneity, in isolation, is inadequate justification for pooling data, because clinical heterogeneity must be low as well.
** Trials that were stopped early due to harm would, presumably, have showed just as much or more harmful effect had they continued to completion. Had the full complement of subjects been enrolled for instance in the ATLANTIS-B trial there would have been 968 subjects rather than 613. The additional 355 subjects would have made the results of the trial statistically more powerful and therefore would have more forcefully counterbalanced the benefits from trials suggesting benefit (both of which were run to completion). The lack of completion of 5 trials because of harms therefore creates an irreversible bias in any data review, whereby the trials that suggest benefit are completed, and become more statistically powerful, while the impact of trials that show harmful effects are weakened.
Caveats: There is a Cochrane review that pooled estimates of effect. 17 We do not endorse this choice because of clinical heterogeneity. However, we present the NNT’s from the pooled analysis for the reader's benefit. The Cochrane review suggested a 6% reduction in disability (based on a dichotomy in which a modified Rankin score of 0 or 1 is 'favorable' and 2 or greater is 'unfavorable') with thrombolytics. This would mean that 17 were treated for every 1 avoiding an unfavorable outcome. The review also noted a 1% increase in mortality (1 in 100 patients die because of thrombolytics) and a 5% increase in nonfatal intracranial hemorrhage (1 in 20), for a total of 6% harmed (1 in 17 suffers death or brain hemorrhage).
It has been argued that the difference between studies suggesting benefit and all other studies is the timing of the intervention. The Cochrane findings do not support this view, nor does one extensive post-hoc analysis.13 More importantly, the most recent study (ECASS-3) suggested benefits when thrombolytics were administered between 3 and 4.5 hours. This is outside the window that purportedly distinguished the NINDS trials, and effectively neutralizes time as the defining factor that separates trials concluding benefit from those that do not.
It has also been noted that differing agents have been utilized in trials, including streptokinase and urokinase and t-Pa. There is no theoretical basis, nor any clinical data from the thrombolytics for MI, that would suggest that t-Pa is less likely to cause ICH or more likely to demonstrate benefit, than any other agent.
Author: David Newman, MD
Published/Updated: March 25, 2013
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