--- Jeff Brosius <[EMAIL PROTECTED]> wrote: > To: "Paramedicine List" <[EMAIL PROTECTED]> > > Pursuant to the recent discussion on thrombolytics and CVA. > > Enjoy the reading. > > Best, > > Jeff Brosius > Paramedic, etc. > Atlanta, GA > www.prehospital-perspective.com > [EMAIL PROTECTED] > "The fate of the wounded rest > in the hands of the one that > applies the first dressing." > -- Nicholas Senn, 1896 > > > ----- Original Message ----- > From: "Jeffrey Mann" <[EMAIL PROTECTED]> > To: <[EMAIL PROTECTED]> > Sent: Thursday, May 16, 2002 6:39 PM > Subject: [EMED-L] An open letter to the stroke interventionist > community regarding tPA for acute ischemic stroke > >
From: "Jeffrey Mann" <[EMAIL PROTECTED]> To: <[EMAIL PROTECTED]> Sent: Thursday, May 16, 2002 6:39 PM Subject: [EMED-L] An open letter to the stroke interventionist community regarding tPA for acute ischemic stroke The debate about the risk:benefit ratio of tPA therapy in acute ischemic stroke continues. Read the following dialogue articles in the May 2002 issue of the Western Journal of Medicine. 1) Truth about the NINDS study: setting the record straight - Jeffrey Mann Available at http://www.ewjm.com/cgi/content/full/176/3/192 2) Why were the benefits of plasminogen activator (tPA) exaggerated? - Griffin Trotter Available at http://www.ewjm.com/cgi/content/full/176/3/194 3) Thrombolysis for acute ischemic stroke: still a treatment for the few by the few - Joanna M Wardlaw, Richard I Lindley, Steff Lewis Available at http://www.ewjm.com/cgi/content/full/176/3/198 The NINDS trial is the only RCT that has shown any benefit from tPA therapy and many clinicians have questioned the validity of the NINDS trial for a number of reasons -- that all the other RCTs have failed to demonstrate the efficacy of tPA, that the NINDS trial's results could possibly be due to chance [1], that the NINDS trial was far too small in size, that the NINDS trial's results are not readily transferable to clinical practice because 50% of the patients were treated in < 90 minutes (a level of clinical performance that is unlikely to be achievable in community practice), and that certain post-marketing studies have shown higher rates of secondary ICH in community practice, which may/may not be due to protocol violations. However, despite these various criticisms, no one has suggested that the NINDS trial is internally invalid because of methodological or interpretative flaws. My personal analysis of the NINDS trial suggests that the NINDS trial, as originally reported in the NEJM, is internally invalid. When I originally wrote my dialogue piece about 9 months ago, I wondered to what degree the imbalance in baseline stroke severity between the tPA-treated patients and the placebo patients in the NINDS trial's 91-180 minutes groups, could account for the favorable results of the NINDS trial -- and I therefore wondered to what degree the NINDS trial could be perceived to be internally invalid. The answer is still not entirely clear to me, and I wonder how clear it will be to the stroke interventionist community after they read my dialogue piece in the wjm. In the original NEJM paper, the NINDS trialists gave no indication that there was any imbalance in baseline stroke severity between the tPA-treated and placebo patients. They also did not comment on the unexpected fact that the odds ratio (OR) for an excellent stroke outcome was 1.7 (mRS<=1) for the 0-90 minutes groups and 2.4 (mRS<=1) for the 91-180 minutes groups, which suggested that tPA was more effective if given later, rather than earlier. The NINDS trialists were obviously disconcerted by this finding, and they continued to analyse their data in private (interestingly, although they generated many hypotheses to account for the unexpected finding, it was obviously due to the fact that they did not correct for the imbalance in baseline stroke severity between the treated and placebo patients). Five years later, the NINDS trialists supplied new figures for the ORs based on a re-analysis of their raw data using an unspecified statistical adjustment for baseline NIHSS scores and other baseline variables - in the article by Marler [2]. However, they only supplied a revised OR for the global statistic stroke outcome measure, and they apparently never published revised OR figures for the most commonly used stroke outcome measure - the modified Rankin score (mRS<=1). Without knowing the revised OR for a mRS<=1, how can a stroke interventionist compare the revised results to the original OR for a mRS<=1, or to the excellent stroke outcome results obtained from other stroke trials, which are usually reported as mRS<=1? Without understanding the statistical adjustment that the NINDS trialists used to create their revised OR figures, how can a stroke interventionist determine whether it adequately corrected for the confounding variable of imbalances in baseline stroke severity? According to the TOAST study [3], the graphical curve delineating the natural relationship between baseline stroke severity and the rate of excellent stroke outcome in untreated stroke patients is very steep, and each one point change in baseline NIHSS stroke severity score could cause a 5-10% difference in the absolute rate of an excellent stroke outcome due to the natural course of the disease. Therefore, any statistical adjustment that the NINDS statisticians used to correct for imbalances in baseline stroke severity has to be fully compatible with that fact. It would be extremely useful if the NINDS statisticians publicise the methodology of their statistical adjustment, so that other independent statisticians can judge whether it is compatible with the TOAST graph. In that same Marler article [2], the NINDS trialists plotted the re-estimated efficacy of tPA against time-to-treatment as a hypothetical model graph-curve (figure 2) and it can be seen that tPA has borderline-positive efficacy after 150 minutes, and the lower boundary of the 95% confidence interval line intersects the "no benefit for tPA" X axis at 150 minutes (see reference number [4] for a hand-drawn copy of figure 2 - the copy is freely viewable online). That model graph-curve suggests that tPA has limited (and equivocal) efficacy after 150 minutes, which would be compatible with Jerome Hoffmann's observation [5] that "the study showed an overall 11-13% absolute benefit with tPA treatment; however, a recent report [2] by the NINDS authors clarified that the benefits were greater than this in the "very early" (0-90 min) group, which means that they had to be less than this in the "early" (90-180 min) group". Also, the fact that the lower boundary of the 95% confidence interval crosses the "no benefit for tPA" X axis at 150 minutes strongly suggests that the NINDS trial's sample size was too small. Gordon Guyatt states in JAMA's Users' Guides to the Medical Literature [6] "In a positive trial establishing that the effect of treatment is greater than zero, look at the lower boundary of the confidence interval to determine whether the sample size has been adequate. If this lower boundary - the smallest plausible treatment effect compatible with the data - is greater than the smallest difference that you consider important, the sample size is adequate and the trial is definitive. If the lower boundary is less than this smallest important difference, the trial is non-definitive and further trials are required". Does the stroke interventionist community fully understand how that hypothetical model graph was devised, and whether it is statistically valid and accurate? Should the NINDS trialists have plotted the model graph using the OR for the most frequently used favorable stroke outcome measure - the mRS<=1 (instead of the global statistic)? What would the revised efficacy figures be if the NINDS trialists had used relative risk measurements rather than odds ratio measurements to quantify the benefit of tPA therapy - after adjusting for imbalances in baseline variables? Barbara Tilley, the primary statistician for the NINDS trial, co-wrote in an article [7] that "odds ratios have been used extensively in data collected both prospectively (for example, a cohort study) or retrospectively (for example, a case control study) when logistic regression is used to adjust for covariates. However, the odds ratio is less commonly used to communicate the primary results of a clinical trial because of its lack of clinical interpretation. It measures neither a relative size nor an absolute size difference for the treatment effect on the outcome. As an alternative, the relative risk (RR), unlike the odds ratio, measures the relative size of the treatment difference, that is, the ratio of the response probability in a treatment group versus the response probability in a reference group." In that same article, Barbara Tilley re-analysed the NINDS trial's data using a log link model rather than a logit link model, and found that the log link model estimated the benefit of tPA to be 1.32 (relative risk estimate) for part II of the NINDS trial while the logit link model had previously estimated the benefit of tPA to be 1.73 (odds ratio estimate). In fact, Barbara Tilley wrote further "Considering the NINDS t-PA stroke trial, if the analysis plan had specified a goodness-of-link test to choose the link function, we would have conducted the global test for the treatment effect based on the log link rather than the logit link. We could then interpret the results using an estimate of relative risk instead of the odds ratio, -----". It is refreshing to note that the NINDS statisticians agree that it is better to use relative risk measurements, rather than odds ratio measurements, to determine the efficacy of tPA, and it is interesting to see how much lower the RR figure is than the OR figure. Although I am very sceptical of the accuracy of the RR figure of 1.32 (because the NINDS statisticians gave no indication that major statistical adjustments were needed to correct for imbalances in baseline stroke severity between the treated and placebo patients) note that the RR figure of 1.32 was for the entire time span of 0-180 minutes. Can you imagine, after examining the graph in reference number 4, how low the RR figure must be for patients treated between 91-180 minutes, and particularly between 150-180 minutes? The relative benefit of tPA for patients treated in the 91-180 time period may only be a fraction of the benefit experienced by patients treated in the 0-90 time period (the estimation of relative benefit is based on the simple awareness that most of the patients treated in the 0-90 minute time period were treated between 60-90 minutes and the estimated odds ratio for a favorable stroke outcome is 2.8-3.8 for that time period, while the estimated odds ratio for the 91-180 time period is between 1.3-2.8, and most of those patients were actually treated between 150-180 minutes and the estimated odds ratio was 1.3-1.8 for the 150-180 time period -- note that all of the estimated odds ratio figures are derived from the Marler graph (reference number [4]). If one cannot precisely determine the adjusted RRR for patients treated between 91-180 minutes, then one cannot precisely calculate the absolute risk reduction (risk difference) for those patients. Barbara Tilley wrote [7] a "risk difference (RD) is the difference in response probabilities between two groups, which is sometimes considered clinically more interpretable than the relative risk, because it indicates an absolute but not relative treatment size difference in response probability. It is an intuitively appealing measure of treatment efficacy in clinical trials. The risk difference is useful in that it provides an estimated amount by which a particular response might be increased or reduced if a specified treatment is removed, and is a particularly important concept when treatment benefits are offset by side-effects and/or by a high cost." In other words, Barbara Tilley is suggesting that one needs to know the absolute benefit of tPA therapy (RD) in order to calculate a risk:benefit ratio for tPA therapy. I agree - but how can a stroke interventionist determine the risk:benefit ratio of tPA therapy for stroke patients treated between 91-180 minutes, assuming that the absolute risk of a major side-effect (symptomatic ICH) is approximately 6%, if he does not precisely know the absolute benefit of tPA therapy for those same patients (after having to make precise statistical adjustments to correct for imbalances in baseline stroke severity between treated and placebo patients)? Also, any absolute benefit figure that is used for the 91-180 minute time span would only be an "average" figure and one really needs to know the absolute benefit for different time spans throughout that 90 minute time period (eg. 90-120 minutes, 120-150 minutes, 150-180 minutes) because the efficacy of tPA continuously wanes throughout the 91-180 minute time period. (To better appreciate the varying relationship between RRR and the NNT with respect to variations in time-to-treatment and/or variations in baseline stroke severity, see reference number [8] which is freely available online) Should stroke interventionists be obliged to offer the stroke patient more precise information about the risks and benefit of tPA therapy - with particular attention paid to natural variations in baseline stroke severity and "real life" variations in time-to-treament? For instance, what are the answers to the following three questions with reference to 4 hypothetical stroke patients? Patient 1 = baseline NIHSS score of 8. Patient 2 = baseline NIHSS score of 12. Patient 3 = baseline NIHSS score of 16. Patient 4 = baseline NIHSS score of 20. Question 1: What is the likelihood of an excellent stroke outcome (mRS<=1) without any treatment for those 4 patients? Question 2: What is the likely benefit of tPA therapy for those 4 patients if they are treated in the following time frames = < 90 minutes, 90-120 minutes, 120-150 minutes and 150-180 minutes? Question 3: What is the likely secondary ICH rate for those 4 patients if they are treated in the following time frames = < 90 minutes, 90-120 minutes, 120-150 minutes and 150-180 minutes? How do you answer question number 1? I believe that the answer to question number 1 has to take the natural course of the disease into precise account, and it is well known that patients with mild strokes have a much better rate of excellent stroke outcome than patients with severe strokes (due to the natural course of the disease). My "best guess" answer to question number 1 is:- Expected rate of excellent stroke outcome for patient number 1 (baseline NIHSS score of 8) = 56% Expected rate of excellent stroke outcome for patient number 2 (baseline NIHSS score of 12) = 42% Expected rate of excellent stroke outcome for patient number 3 (baseline NIHSS score of 16) = 23% Expected rate of excellent stroke outcome for patient number 4 (baseline NIHSS score of 20) = 13% The "expected" rate of excellent stroke outcome numbers come from the TOAST graph curve [3]. Do you use different "expected" figures? >From where do you obtain your "expected" figures? I believe that a stroke interventionist should be able to supply a stroke patient with a numerical figure for the expected rate of excellent stroke outcome - derived from the evidence-based medical literature - so that the individual stroke patient can estimate his likelihood of an excellent stroke recovery (based on the natural course of the disease) before he tries to establish whether tPA therapy (or any other stroke therapy) can offer him a better rate of recovery. If the stroke interventionist community does not agree with the estimated figures from the TOAST graph, then why does it not perform a prospective study on 10,000 acute ischemic stroke patients (untreated) and measure their baseline NIHSS stroke severity scores and their rate of excellent stroke outcome at 3 months? It would then be possible to draw a TOAST-like graph showing the precise relationship between the baseline NIHSS score and the rate of excellent stroke outcome without having to use a logistic regression equation to draw a "best-fit" graph (because the graph would be plotted from actual baseline NIHSS scores for each level of baseline stroke severity from a NIHSS score of 1-25). By plotting that graph, the stroke interventionist community would have established a "gold standard" curve that would allow it to determine the true benefit of tPA therapy (or any other stroke therapy) - by comparing the individual treated patient's results to the "gold standard" graph. How do you answer question number 2? I believe, that in the absence of reliable results from a RCT that is perfectly randomized for baseline stroke severity, that one can only answer question 2 accuratedly if one plots the results of tPA therapy for different treatment times (<90 minutes, 90-120 minutes, 120-150 minutes, 150-180 minutes) for each level of baseline stroke severity (from a NIHSS score of 1-25) on top of that "gold standard" graph, so that an automatic correction is made for imbalances in baseline stroke severity. If the tPA-treated patient's rate of excellent stroke outcome figure is higher than the untreated patient's figure (for each baseline NIHSS score), then tPA obviously works, and the degree of efficacy will be obvious by seeing how much higher the treated patient's figure is above the untreated patient's "gold standard" figure - for varying baseline stroke severity scores and varying times-to-treatment. How do you answer question number 3? I believe that one can really only answer question 3 accuratedly if the stroke interventionist community plots the secondary ICH rate results similarly - by plotting the secondary ICH rate against the baseline NIHSS score and by plotting 4 sets of curves for the different treatment times - because it is well-known that the secondary ICH rate depends on both the baseline stroke severity and the degree of delay in administering tPA therapy. Kidwell [9] showed that the secondary ICH rate increased markedly with baseline NIHSS scores 10, but their published results are of limited value because the study sample size was too small, because they used IA tPA, and because they used a subgroup analysis with subgroups that are too broad (see reference number [8] for a handpainted copy of their diagram showing the hemorrhagic transformation results - it is freely viewable online). I think that the ICH rate needs to be plotted for each NIHSS score between 1-25 (and not from limited subgroup data, which is too crudely inaccurate) and for varying treatment times. The result-analysis may show that patients with severe strokes (NIHSS score 15), who are treated later ( 150 minutes after stroke onset), have much higher secondary ICH rates and that the risk:benefit ratio of tPA therapy for those patients is significantly greater than 1.0. The stroke interventionist community already has enough pooled data from a number of stroke trials [10] to be able to plot those curves. By using the pooled data to plot those curves, the variable of imbalances in baseline stroke severity will no longer have to be considered a confounding variable, and the true risk:benefit ratio of tPA therapy will immediately become apparent -- by examining the excellent stroke outcome rate and the secondary ICH rate for each baseline NIHSS score for a variety of treatment times (< 90 minutes, 90-120 minutes, 120-150 minutes, 150-180 minutes). "Statistics are like a bikini: what they reveal is suggestive, but what they conceal is vital" - Aaron Levenstein. I think that the stroke research community needs to immediately make the pooled raw data from all the tPA-for-stroke trials publically available, so that the vital truth about tPA can be revealed. The vital truth regarding tPA's efficacy in acute ischemic stroke cannot be discovered by examining the result-analyses of the major tPA-for-stroke RCTs (NINDS, ECASS, ECASS II, ATLANTIS) as they were originally reported in the medical literature, because they did not address the confounding effect of the most critical prognostic variable - imbalances in baseline stroke severity between the tPA-treated and placebo patients. Even more recent post hoc re-analyses of those trials, such as the re-analysis of the ATLANTIS trial's < 3 hours patient group [11] and the meta-analysis of the NINDS, ECASS, ECASS II and ATLANTIS trials [12] make no attempt to correct for imbalances in stroke severity between the treated and placebo patients, thereby rendering their conclusions moot. I think that if the stroke interventionist community decides that the NINDS trial was too small in size and too poorly randomized, and that arbitrary, and inordinately complex, post hoc statistical adjustments cannot accurately correct for the marked imbalance in baseline stroke severity in the 91-180 minutes groups -- then the need to perform a much larger tPA-for-stroke RCT, that is precisely balanced for critical prognostic variables like baseline stroke severity, becomes imperative. The stroke research community may decide to actively debate the issues that I have discussed, but if genuine "uncertainty" still persists, then the need to perform a new RCT will likely remain -- because it makes no sense to base an entire "brain attack" industry on the results of a single clinical trial, if its legitimacy remains forever controversial and doubtful. In the interim period, the stroke interventionist community could debate what to do with the presently accumulated raw data, and it could also debate the advisability, and correct methodology, of analysing the pooled raw data from multiple RCTs and observational studies (as I have just described). Finally, I think that stroke researchers, who deem themselves tPA-experts, should actively engage tPA-contrarians and tPA-sceptics in "open" scientific debate regarding the utility of tPA in acute ischemic stroke. The tPA-experts should specifically avoid adopting an "all-knowing" attitude as exemplified by the statement made by James Grotta in his editorial in the February 2002 issue of the Stroke Interventionalist publication [13], when he wrote "The data supporting the efficacy of thrombolysis within the first 3 hours after stroke onset in patients who qualify, as nicely reviewed by Dr Pancioli, is now unanimously endorsed by those who know best - ie. those Neurologists and Emergency Physicians who have made the comittment to take care of acute stroke patients for a living and are experienced in using thrombolytics." The implication of that statement seems to be that other neurologists and emergency physicians, who do not actively participate in stroke research, are incapable of accurately analysing the evidence-based medical literature, and they should remain passively dependent on the subjective judgments of "those who know best". The stroke experts are obviously at the cutting edge of stroke research, and they are the people most keenly aware of potentially productive research endeavours in the area of biological and mechanical thrombolysis. However, I don't agree that stroke experts are automatically more adept at judiciously assessing the "weight" of the published tPA-for-stroke medical literature, and that they will automatically come to a more rational and better balanced conclusion. It is my personal belief that any conscientious physician, who has acquired a modicum of evidence-based medicine skills, can painstakingly review the tPA-for-stroke medical literature and come to independent judgments, that may be closer to the vital truth than the biased judgments of some of the self-appointed tPA-experts. History, of course, will be the final arbiter, and the future will determine who is closer to realizing the vital truth about tPA therapy in acute ischemic stroke -- the tPA-experts, who have a fixed set of a priori biases, and who are therefore absolutely convinced that they know best, or the tPA-sceptics who are likely to remain more open-minded about the issues. Jeff Mann. References: 1. Carl E Counsell, Mike J Clarke, Jim Slattery, Peter A G Sandercock. The miracle of DICE therapy for acute stroke: fact or fictional product of subgroup analysis? BMJ 1994;309:1677-1681 (24 December). Available online at http://bmj.com/cgi/content/full/309/6970/1677 2. Marler, J R. MD. Tilley, B. C. PhD. Lu, M. PhD. Brott, T.G. MD. Lyden, P. C. MD. Grotta, J. C. MD. Boderick, J. P. MD. Levine, S. R. MD. Frankel, M.P. MD. Horowitz, S. H. MD. Haley, E. C. Jr. MD. Lewandowski, C. A. Kwiatkowski, T. P. MD. for the NINDS rt-PA Stroke Study Group *. Early Stroke Treatment Associated With Better Stroke Outcome: The NINDS rt-PA Stroke Study. Neurology 55 (11) 1649 - 1655, December 12, 2000. 3. Adams, H. P. Jr. MD. Davis, P. H. MD. Leira, E. C. MD. Chang, K.-C. MD. Bendixen, B. H. PhD, MD. Clarke, W. R. PhD. Woolson, R. F. PhD. Hansen, M. D. MS. Baseline NIH Stroke Scale score strongly predicts outcome after stroke: A report of the Trial of Org 10172 in Acute Stroke Treatment (TOAST). Neurology. 53(1):126-131, July 13, 1999 4. Representative copy of figure 2 from the Marler article. Available online at http://emguidemaps.homestead.com/files/marlergraph.html 5. Hoffmann. J.R. Tissue Plasminogen Activator for Acute Ischemic Stroke: Is the CAEP position statement too negative? CJEM vol 3 number 3 July 2001. Available at http://www.caep.ca/004.cjem-jcmu/004-00.cjem/vol-3.2001/v33-183.htm#main 6. Users' Guides to the Medical Literature: A Manual for Evidence-based Clinical Practice - page 348 - edited by Gordon Guyatt, Drummond Rennie. 7. Lu M, Tilley B. Use of odds ratio or relative risk to measure a treatment effect in clinical trials with multiple correlated binary outcomes: data from the NINDS trial. Statistics in Medicine 2001; 20: 1891-1901. 8. Relationship between baseline risk of a poor stroke outcome and the RRR and the NNT Available online at http://emguidemaps.homestead.com/files/nnttpa.html 9. Kidwell, Chelsea S. MD; Saver, Jeffrey L. MD; Carneado, Joaquin MD; Sayre, James PhD; Starkman, Sidney MD; et al. Predictors of Hemorrhagic Transformation in Patients Receiving Intra-Arterial Thrombolysis. Stroke. 33(3):717-724, March 2002. 10. Saver JL, Kidwell CS, Starkman S. Commentary: Thrombolysis in stroke: it works! BMJ 2002;324:723-729 (23 March). 11. Albers, Gregory W. MD. Clark, Wayne M. MD. Madden, Kenneth P. MD, PhD. Hamilton, Scott A. PhD. ATLANTIS Trial: Results for Patients Treated Within 3 Hours of Stroke Onset. Stroke. 33(2):493-496, February 2002. 12. Fisher, Marc MD; Ringleb, P. A. MD; Schellinger, P. D. MD; Schranz,C. MD; Hacke, W. PhD, MD Thrombolytic Therapy Within 3 to 6 Hours After Onset of Ischemic Stroke: Useful or Harmful? Stroke. 33(5):1437-1441, May 2002. 13. The Stroke Interventionalist publication - February 2002 issue. Available at http://www.thestrokegroup.com/tsi/pdfs/TSI_24.pdf __________________________________________________ Do You Yahoo!? LAUNCH - Your Yahoo! Music Experience http://launch.yahoo.com
