DEPARTMENT OF HEALTH AND HUMAN SERVICES

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FOOD AND DRUG ADMINISTRATION

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CENTER FOR DRUG EVALUATION AND RESEARCH

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CARDIOVASCULAR AND RENAL DRUGS ADVISORY COMMITTEE

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90TH MEETING

TUESDAY,
MAY 2, 2000

		The committee met at 9:00 a.m. in the Masur Auditorium of the National Institutes of Health, Building 10, 900 Rockville Pike, Rockville, Maryland, Dr. Milton Packer, Chairperson, presiding.

PRESENT:

Milton Packer, M.D., Chairperson
Robert Califf, M.D., Member
John DiMarco, M.D., Member
Marvin Konstam, M.D., Member
Thomas Graboys, M.D., Consumer Representative
Ileana Piña, M.D., Member
Joan C. Standaert, Executive Secretary

PARTICIPANTS:

Paul Armstrong, M.D.
Jeffrey Borer, M.D.
Thomas Fleming, Ph.D.
Cindy Grines, M.D.
Joann Lindenfeld, M.D.

FDA

Ann Farrell, M.D.
Florence Houn, M.D.
Robert O'Neill, M.D.
Thomas Permutt, Ph.D.
Mushifiqur Rashid, Ph.D.
Lilia Talarico, M.D.
Sue-Jane Wang, Ph.D.

SPONSOR REPRESENTATIVES:

Lloyd Fisher, Ph.D.
Jack Hirsh, M.D.
Gary Koch, Ph.D.
Matthias Luz, M.D.
Salim Yusuf, D. Phil., M.D.

A-G-E-N-D-A
Page

Open Session

Call to Order: Welcome and Information
Chairman, Milton Packer, M.D.	4

Conflict of Interest Statement,
Joan Standaert, Executive Secretary	4

Open Public Hearing - Scientific presentation of the open session will begin once last open hearing participant has spoken.	7

NDA 20-807/S-004, Refludan (lepirudin), Aventis Pharmaceuticals, Inc., to be indicated as an anticoagulant in adult patients with acute coronary syndromes (unstable angina and acute MI without ST segment elevation on ECG)	.7

Presentation - Aventis Pharmaceuticals, Inc.:

Introduction, Matthias Luz, M.D.	7

Clinical Efficacy Data, 
Salim Yusuf, D.Phil., M.D.	30

Putative Placebo Control, Lloyd Fisher, Ph.D.	175

Statistical Review, Thomas Permutt, Ph.D.	195
                    Sue-Jane Wang, Ph.D.	204

Clinical Safety Data, Matthias Luz, M.D.	246

Summary of Clinical Evaluation, Jack Hirsh, M.D.	271

Questions and vote	281

Adjournment	299

P-R-O-C-E-E-D-I-N-G-S
9:00 a.m.
		DR. PACKER:  Good morning.  I'd like to call to order the 90th meeting of the Cardiovascular and Renal Drugs Advisory Committee.  This is the second day of a two-day meeting and we will ask Joan Standaert to read the conflict of interest statement for this morning's session.
		Joan.
		MS. STANDAERT:  The following announcement addresses the issue of conflict of interest with regard to this meeting and is made a part of the record to preclude even the appearance of such at this meeting.
		Based on the submitted agenda and information provided by the participants, the agency has determined that all reported interest and firms regulated by the Center for Drug Evaluation and Research present no potential for a conflict of interest at this meeting with the following exceptions.
		Dr. Udho Tadani has been excluded from participating in today's discussion and vote concerning Refludan.
		Further, in accordance with 18 U.S.C. 208(b) full waivers have been granted to Drs. Cindy Grines, Ileana Piña, Robert Califf, Jeffrey Borer, Marvin Konstam, Milton Packer, and Paul Armstrong.
Copies of these waiver statements may be obtained by submitting a written request to FDA's Freedom of Information Office located in room 12A30 of the Parklawn Building.
		In addition, we would like to disclose for the record that Drs. Jeffrey Borer, Robert Califf, and Cindy Grines have interest which do not constitute financial interest within the meaning of 18 U.S.C. 208(a) but which could create the appearance of a conflict.  The agency has determined notwithstanding these interest that the interest of the Government in their participation outweighs the concern that the integrity of the agency's programs and operations may be questioned.  Therefore, Drs. Jeffrey Borer, Robert Califf, and Cindy Grines may participate fully in all  matters relating to Refludan.
		In the event that the discussions involve any other products or firms not already on the agenda for which an FDA participate has a financial interest, the participants are aware of the need to exclude themselves from such involvement and their exclusion will be noted for the record.
		With respect to all other participants, we ask in the interest of fairness that they address any current or previous financial involvement with any firm whose products they may wish to comment upon.
		That concludes the conflict of interest statement.  I would like to make just one public service announcement.  The management of the auditorium has asked me to remind individuals that no food is permitted in the auditorium and that you are to please take all your papers and belongs with you when you leave.  Thank you.
		DR. PACKER:  Thank you very much, Joan.  The topic for today is NDA 20-807/S-004, Refludan or lepirudin.  The sponsor is Aventis Pharmaceutical Company.  The indication that is being pursued is as an anticoagulant in adult patients with acute coronary syndromes.  
		In the matter being brought to the committee today, the Cardiovascular and Renal Drugs Advisory Committee is acting in a consultant capacity to the Coagulation Drug Products Division and consequently this is not an unusual occurrence.  We have acted as a consultant committee when there is a major cardiovascular indication which is being pursued even outside the Division of Cardiovascular and Renal Drugs.
		Without any further ado, we'll ask the sponsor, Aventis Pharmaceuticals, to being their presentation.  I'm so sorry.  It is traditional to ask whether there is any public comment.  There being no public comment, with due apologies I'll ask the sponsor to begin their presentation.
		DR. LUZ:  Good morning, Mr. Chairman, ladies and gentlemen.  I'm Matthias Luz, the global project leader and global clinical manager for the lepirudin or Refludan at Aventis.
		It is my pleasure to come before this committee today along with my colleagues to share with you the results of the OASIS studies and discuss the use of lepirudin in unstable angina or acute MI without ST elevation.  More shortly, acute coronary syndromes or ACS.
		The agenda will be as follows.  In my introductory talk I will give you a brief overview of the regulatory history and principal pharmaceutical properties of the drug, introduce the rationale for its use in ACS, and briefly review several aspects of the clinical trials that are of relevance to the understanding of the presentations and interpretation of the results.
	      Next Dr. Salim Yusuf will present the clinical efficacy data of the OASIS studies.  Dr. Yusuf is a Professor of Cardiology at the McMaster University in Hamilton, Canada, and the chairman of the OASIS steering committees.
		The next speaker will be Dr. Lloyd Fisher.  Dr. Fisher is a Professor Emeritus of Biostatistics at the University of Washington.  He will discuss how lepirudin might have fared had we been able to compare lepirudin plus aspirin versus aspirin alone as opposed to heparin plus aspirin.
		We view this comparison as an integral part of the submission since first the U.S. regulatory standard for the approval of new drugs is that the new drug has to convincingly be placebo and, second, heparin is not approved in ACS.
		I will then be presenting the clinical safety data.  Finally, Dr. Jack Hirsh will summarize the clinical evaluation.  Dr. Hirsh is a Professor of Medicine also at the McMaster University in Hamilton, Canada, and the chairman of the OASIS-2 Data and Safety Monitoring Board.
		For the discussion of specific statistical aspects, we also have Dr. Gary Koch who is a Professor of Biostatistics at the University of North Carolina, and Dr. Larry Roi who is the project statistician for lepirudin available.
		I will be available to moderate questions as needed.
		Refludan was approved in the United States in March 1998 for the treatment of patients with heparin-induced thrombocytopenia and thromboembolic complications.  Since then the drug has also been approved in Canada, all 15 countries of the European union, and 15 further countries.
		Post-marketing experience is available from an estimated 5,000 patients worldwide.  Specific information has been collected through an extensive two-year drug monitoring program in the European union that involved approximately 1,300 patients and constitutes the largest prospectively collected database in heparin-induced thrombocytopenia.
Importantly, the dose used in HIT is identical to the dose that is proposed for the new indication.
		Based on the findings of the OASIS studies, we propose that the following new indication be approved.  Refludan as indicated for anticoagulation in adult patients with acute coronary syndromes, ACS, unstable angina or acute MI without ST elevation.
		In this setting Refludan has been shown to decrease the rate of CV death or new MI combined double endpoint, as well as the rate of CV death, new MI or refractory angina combined triple endpoint.  Of note, the two endpoints mentioned were the primary and key secondary endpoint of the OASIS-2 study that forms the principal basis of this submission.
		The rational for use of lepirudin in ACS is derived from the pathophysiology of the disease and the pharmacological properties of the drug.  Acute coronary syndromes are caused by plaque instability or rupture leading to activation of blood coagulation.  This, in turn, leads to complete or partial exclusion of the coronary arteries.
		Thrombin has been identified as playing a key role in the pathogenesis of ACS.  Hirudin as the most potent and specific thrombin inhibitor known can, therefore, be expected to have a great potential in drug therapy of ACS.
		Natural hirudin is produced by the saliva glands of the medicinal leech.  Lepirudin is a recombinant hirudin that is derived from transfected yeast cells.
		This slide summarizes and illustrates the most important mechanistic differences between heparin as an indirect thrombin inhibitor and lepirudin as a direct thrombin inhibitor.  Let me walk you through this slide.
		In the top right-hand part you see a very schematic presentation of a thrombin molecule with the catalytic or active site, the heparin binding site, and the fibrin binding site.  Lepirudin binds to both the active side and the fibrin binding site of the thrombin molecule.
		Since its affinity thrombin is higher than that of fibrin, it is able to find to thrombin even in the presence of fibrin.  Therefore, both fluid phase and clot-bound thrombin can be inhibited by lepirudin.
In contrast, heparin binds to the heparin binding site of thrombin.
		In the presence of fibrin, thrombin is held in a tight turnery complex with heparin and fibrin.  In this situation heparin in the active heparin AT-III complex cannot access the heparin binding site of the thrombin molecule.  Therefore, clot-bound thrombin is prevented from inhibition by heparin.
		The clinical pharmacology of lepirudin was extensively discussed in the original application for HIT.  This slide just briefly summarizes the key pharmacokinetics features.  After IV administration, the drug is rapidly distributed to the extracellular compartment.  Clearance occurs mainly by the kidneys, the terminal half-life ranging between 0.8 and 2.0 hours after IV infusion.  	Of note, consistent with the primary elimination pathway decreased renal function leads to a prolonged half-life.
		The basis of the submission or the OASIS-1 and OASIS-2 studies, in particular the 10,000 patients that OASIS-2 study.  The entire program additionally involves two small early Phase IIa feasibility studies that were submitted with the original application for HIT and will not further be discussed during today's presentations.
		In the following several slides, I will review the active heparin that was used as the control in both OASIS studies.  The U.S. regulatory standard and preferred control is placebo.  Although no active drug except aspirin) was approved for use in ACS before the OASIS studies were conducted, heparin was widely accepted as the standard of care.
		This clinical approach was justified in 1996 by a meta-analysis performed and published by Oler and colleagues.  This meta-analysis is an overview of six randomized trials comparing heparin plus aspirin versus aspirin alone in a total of slightly over 1,300 patients.
		Dr. Fisher will talk about the results in greater detail in his presentation.
		Briefly, the Oler meta-analysis showed that the combination of heparin and aspirin led to a 33 percent reduction in the occurrence of all-cause death or MI during randomized treatment as compared to aspirin alone.  This result of borderline significant at a p level of .06.
		Five out of the six studies included in the Oler meta-analysis used a heparin regimen consisting of initial IV bolus that was followed by a constant IV infusion.
		One study used a regimen of intermittent high dose IV boluses.  The dose of the initial bolus ranged between 5,000 and 7,500 units and that of the infusion ranged between 1,000 and 1,250 units per hour.
		In the study that used intermittent boluses, the dose that was given during the first 24 hours gives us an average hourly rate of 1,650 units.  During the following four days of treatment in this study, the dose was markedly reduced and averaged to about 1,250 units per hour.
		In the OASIS studies we also used a bolus infusion regimen for heparin.  In both studies the initial bolus consisted of 5,000 units.  In OASIS-1 the protocol stipulated an infusion dose of 1,000 units per kilogram for patients up to the weight of 60 kilograms and 1,200 units per hour in patients weighing more than 60 kilograms.
		In contrast, OASIS-2 used a fully weight-adjusted regimen of 15 units per kilogram an hour.  Importantly, the average dose actually given in the trials was almost identical in the range of 1,120 to 1,170 units.
		This slide shows you how the OASIS heparin regimens compare with the regimens used in other randomized heparin controlled registration studies, namely the ESSENCE study and TIMI-11B study, comparing enoxaparin with unfractionated heparin, the FRIC study comparing dalteparin with unfractionated heparin.
		You will note that the initial bolus was almost identical in all studies.  The TIMI-11B study used the weight-adjusted bolus that at the average weight of 75 kilograms yields almost the same dose as in the other studies.
		Similarly, the infusion doses used in these five studies were, in fact, very close to each other the OASIS studies marking the upper end of the tide range.
		In my last slide I will briefly review the approach to the primary analysis in the OASIS-2 study.  Aventis specified Modified Intention to Treat analysis as the primary analysis in the statistical analysis plan prior to unblinding of the study.  
		The protocol specified in Intention to Treat analysis as primary, and the ITT has had emphasis in FDA review.  Therefore, for the purpose of today's presentation, we will focus on the ITT findings and, in addition, provide some MITT findings.
		You will find the ITT findings also in the appendix to your briefing documents.  Importantly, as Dr. Yusuf will show in his presentation, there are no appreciable differences between ITT and MITT findings.  This is not surprising because among the 10,141 patients enrolled in the OASIS-2 study, the MITT analysis only excludes 61 patients who did never receive study drug and two patients who received study drug but did not have a seven-day assessment.
		Thank you for your attention.
		DR. PACKER:  Before proceeding, let's see if the committee has any questions.  We'll begin with our primary reviewer, Dr. Borer
		DR. BORER:  I'd like to go back to the pharmacokinetics that you presented.  Let me preface my question by telling you why I'm asking.  Several drugs have been approved in the last couple years for treatment of patients with acute coronary syndromes and they are all very potent antithrombotics of one sort or another, generally platelet active.  
		All were approved with the kind of kinetic information that you've presented here and no more.  The result has been that in the percentage of patients, and in your study it's 1.9 percent of patients receiving lepirudin that go emergently to by-pass grafting, the surgeons were left totally unprepared for what then transpired which often was major bleeding.
		You list no bleeding complications in the surgical patients.  We may want to discuss that later on when you get to your safety section, but at least I would like to know now more about kinetics.  You have the terminal plasma half-life here.  Can you tell us something about the binding kinetics with thrombin?  Over what period of time after the drug is stopped will there still be an antithrombotic effect?
		DR. LUZ:  The binding between hirudin and thrombin is essentially an irreversible binding so there will be a continued effect.  At least that is the assumption in the plaque.  With new thrombin generated, this will certainly play a minor role after the elimination of the drug.
		DR. BORER:  So over what period of time is the aPTT still abnormal?  And over what period of time is the bleeding time abnormal?  What period of time are patients at risk from excessive bleeding or abnormal bleeding once the infusion is stopped?
		DR. LUZ:  The aPTT usually returns to normal levels within five to six hours which is consistent with the half-life of the drug.
		DR. CALIFF:  I'm sorry.  Doesn't that depend on renal function in a very strong way?
		DR. LUZ:  It certainly depends on the renal function.  That's why I say usually in patients with normal renal function with the half-life going up.  With impaired renal function one can also expect that the aPTT levels would remain elevated in these patients.
		DR. BORER:  If there was persistent elevation or if somehow we found that there was a proclivity for abnormal bleeding even though the aPTT has begun to come down, is there an appropriate antidote, an appropriate regimen to use?  For example, give fresh/frozen plasma or whatever.  I mean, what would you do if you had to perform an emergency operation?
		DR. LUZ:  To answer your question very specifically, there is no specific antidote available.  There have been various attempts to reverse the hirudin action including certainly the use of fresh/frozen plasma or facta concentrates.   There is no well established concept to reverse the action.  Ultimately, the only way to remove the drug from the circulation would be that the patients undergo hemodialysis.
		DR. BORER:  Okay.  We may come back to this in the safety issues but I would like to at least flag this as an issue now.
		DR. PACKER:  Maybe we should also take the opportunity now to have the committee discuss a little bit the heparin dosing.  We probably will not have a better time than now to do so.  All the discussion moving forward will probably focus on other issues.  		The sponsor has utilized two different -- slightly different heparin dosing in OASIS-1 and in OASIS-2 and the meta-analysis by Oler also used a variety of heparin dosing regimens.  
		The two regimens in OASIS-1 and OASIS-2 titrated the aPTT from 60 to 100 seconds.  I would like to get some discussion in the committee as to the validity or advisability of the heparin dosing is one of the questions that is being posed to the committee.  		Rob, can I start with you?
		DR. CALIFF:  Well, I guess it would be useful to get the sponsor's point of view on what the best interpretation of the best heparin.  I think there are two issues here and I know we're going to come back to this multiple times throughout the day.  		One issue is how does the heparin dose used in this study compare with what is going to be used in the systematic overview to generate this putative placebo. The other question is what the right heparin does.  I know that the new guidelines recommending a lower heparin does and what is in these studies.  It might be useful to hear your point of view as to whether you think this dose use as a control is actually too high.
		Let me just say I haven't been involved in this field for quite a while.  It seems to me the dose you picked at the time you did the study was the dose that the experts recommended.  I don't think there's an argument about whether the dose you picked at the time was one that would have been picked by most people in the field at the time.  The question now is now that the trial is over how do we interpret it in the light of new information.
		DR. LUZ:  Well, there are several aspects.  First, as I showed, the average dose given in the OASIS trial was right in the middle of the range that was used in the Oler meta-analysis.  It also compares in a tight range with the regimens used in other registration studies using heparin as a control.
		If you expand this comparison to studies that use heparin in addition to other drugs or had heparin aboard in some way, you'll find that the range is exactly the same.  There is no difference.
		Second point is that the actual guidelines that were in effect at the time when the OASIS studies suggested an even higher dose consisting of 80 units per kilogram for the bolus and 18 units per kilogram an hour before the infusion.  We were, in fact, below that range.  
		The third point is that the GUSTO-IIa study suggested to some degree that 1,300 units might be too high.  We stopped below that with the dose regimes in the OASIS studies.
		The fourth point might be that with the weight-adjusted regime that was used in the OASIS-2 study, you might expect that patients having a bigger body weight would have higher rates of bleedings because they received more heparin as compared to a fixed dose of 1,000 or 1,100 unit regime.  This, in fact, was not found in the OASIS-2 studies.  The bleeding rates in patients below and above 75 kilograms were identical.
		Apart from that, and Dr. Jack Hirsh could perhaps elaborate on that further, to the best of my knowledge there is no established dose response relationship for heparin that has come out of a randomized trial looking for clinical endpoints.
		DR. CALIFF:  I think that is true.  On the other hand, study after study in the last three or four years has found that patients who do have aPTT greater than 70 to 75 seconds not only have a higher rate of bleeding but a higher rate of ischemic events.
		Again, I'm not questioning the choice of the dose at the time it was done.  What I'm trying to do is get some perspective on how we look at it now that we have a lot more information about heparin.
 		DR. HIRSH:  Rob, can I comment on that?  Actually, I know of no new information since the initial trial was commenced that is at variance with the dose that was selected.  There were two problems.  One is that the bleeding has tended to occur in patients treated with thrombolytic therapies.  Is that not the case?
		DR. CALIFF:  I think there is a much higher rate of bleeding with thrombolytic therapy but even in the nonthrombolytic looking at the TIMI trials and all the GUSTO trials.  Above about 70 seconds there's a pretty dramatic up-slope to the bleeding risk.  Also the surprising increase in ischemic events which none of us expected to see but it's been replicated in about four large trials.
		DR. HIRSH:  I think that the most robust way of looking at heparin is the case rather than the PTT.  The PTT is very tremendous.  The PTT is like the prothrombin time to the INR so that you may have got it in some of the studies but depending on the reagent, a PTT of 60 to 100 would be the same as 40 to 70 with other reagents.  This has been well published.  I think that the best way of looking at it would be dose rather than PTT because, as I said, the PTT varies so much.
		DR. PACKER:  But, Jack, you would say this dose is one that you would recommend today?
		DR. HIRSH:  Yes, based on the data I didn't see any reason why not.
		DR. PACKER:  But the dose is to be titrated to adjust the PTT.
		DR. HIRSH:  Yes, that's the standard approach, to adjust the PTT.  It's a very inexact approach because unlike the prothrombin time, although attempts have been made to standardize the PTT, those attempts have not been widely used.  The fruits of those attempts have not been widely used.  
		If you can recall back to the days 15 years ago when people using a prothrombin time instead of an INR, that's where we stand now with the PTT.  That's why I say I think if one was to look at the best way of comparing dosing regimes, it would be based -- there are three things to look at: the bolus, because that's going to have an early effect because there's always an overshoot; the continuous infusion; and the PTT.  
		I think of those three the PTT is least reliable.  To say that if you go beyond a certain PTT you are going to run into trouble would be the same as saying if you go beyond a certain prothrombin time, you get into trouble.  We know that a prothrombin time with a reagent with an ISI of, say, 2.7, the INR would be about 13 compared to an INR of about three prothrombin time with an ISI of 1.  
		DR. CALIFF:  So the point you're making is that the PTT is not a standardized answer.  There are multiple.
		DR. HIRSH:  That's why I think that PG is not standardized.  The bolus dose is standardized, the continuous infusion is standardized.  It's reasonable, I think, based on local hospital practice to adjust the dose because you're not going to get a very, very precise --
		DR. CALIFF:  But so as not to mislead people, you're not saying that if you give a standardized dose that biological anticoagulant activity is going to be the same from patient to patient.
		DR. HIRSH:  No, it's not.  It's going to be highly variable.
		DR. CALIFF:  Right.  So there are two factors here.  One is the biological variability of what happens to heparin when it gets in the system, and the other is that we have a lousy test to follow it.  Two sources of variability. 
		DR. HIRSH:  So to answer the question, I think that to go back to the original question, whatever dose within the range that was shown that was selected would be reasonable and it would be hard to argue that one dose is better than another dose.
		DR. PACKER:  There has to be a relationship between dose and bleeding.  There is a relationship between dose and bleeding events.
		DR. HIRSH:  Definitely.
		DR. PACKER:  Okay.  Paul.
  		DR. ARMSTRONG:  Jack, just before you leave, let me be clear.  You would advocate a nonweight-adjusted bolus and an infusion as was articulated in OASIS-2 and a PTT target that was the same as in OASIS-2, or would you adjust the PTT target differently now in the light of current information and guidelines or not?  I want to be clear.
		DR. HIRSH:  I'd certainly use the bolus version, the continuous infusion.  I think it's reasonable to use a lower dose in the very light and a higher dose in the very heavy but weight is a fairly weak predictor of response to heparin.  
		When it comes to the PTT, if the mean dose that was used was the same in the various studies, then the PTT response that was -- or the target PTT was a reasonable target PTT if anything was a little higher than would be currently used but certainly not lower.  To answer your question, I would probably go a little lower now except knowing that the mean dose of heparin that was used in the study was really quite low, I don't think they ever shot with PTT.
		DR. PACKER:  Marv.
		DR. KONSTAM:  I would just like to know in OASIS-2 what was the frequency of measuring the PTT?  How often was dosage suggested?
		DR. LUZ:  As per the protocol, it was to be measured six to eight hours after start of the infusion and at least once daily thereafter.  I think the average number of measurements was in the range of six.
		DR. PACKER:  Any other comments?  I think part of the reason we're having all this discussion is that both of the major trials being presented by the sponsor are active comparator trials against the drug which is not approved for the indication which is being presented and for which a dosing regime that optimizes efficacy and safety has not been established and remains a moving target.  I think that it's part of the struggle that we will face today in trying to  decipher risk to benefit relationships.
		Okay, you can proceed.
		DR. LUZ:  Let me introduce Dr. Salim Yusuf, the chairman of the OASIS-1 and 2 steering committees.
		DR. YUSUF:  Mr. Chairman, ladies and gentlemen, on behalf of the OASIS Investigative and Steering Committee it's my pleasure to share with you the results of the two OASIS trials.  OASIS stands for the organization to assess strategies and ischemic syndrome.  
		It's a program of research that consist of three parts.  All three in patients with unstable angina or acute myocardial infarction without significant ST elevation.  
		The first part evaluates the relative efficacy of hirudin versus unfractionated IV heparin and this involved two studies, the OASIS-1 study and the OASIS-2 study.  It also involved the concept of prolonged antithrombotic therapy with warfarin as the standard therapy on top of aspirin as subsidies of these trials.
		A third component looked at the clinical course and practice patterns in multiple countries and data have already been published from 8,000 people from six countries and there are ongoing attempted in several other countries.
		This is the design of OASIS-1.  The study group involved people with unstable MI without ST evaluation, unstable angina or MI without ST elevation.  Patients were randomized to three groups, unfractionated heparin, low dose of lepirudin, and a medium dose of lepirudin.  
		By the statement you would probably recognize there was meant to be a high dose of lepirudin as well.  However, as we were just about to embark on this program, the data from GUSTO-IIa was published and there was concerns of safety at a higher dose of hirudin so it was dropped.
		The study included 909 patients.  There were three major endpoints that the study focused on: cardiovascular death, myocardial infarction, and refractory angina as a composite.  The same composite but stopping at refractory angina and the same composite on cardiovascular death or myocardial infraction.
		The most important endpoint in the study was considered to be the first one simply because it was the highest event rate and because sample size is calculated based on this.  	Although this endpoint is clinically the most relevant, the number of events were expected to be very few in this pilot study.
		The study was a randomized partially study.  Therefore, we ensured a number of steps to ensure there is an unbiased evaluation of the outcome the key component of which was central randomization and central blinded adjudication.
		These were the doses used.  The low dose of hirudin involved a bolus of .2 milligrams per kilogram followed by an infusion of 1 milligram per kilogram per hour for 72 hours.  The medium dose involved a bolus of .4 milligrams per kilogram per hour followed by an infusion of .15 milligrams per kilogram per hour for 72 hours.
		The infractionated dosing regimen was as described by Dr. Matthias Luz so that in those over 60 kilograms 1,200 units an hour was used and those under 60 kilograms a lower dose was used, 1,000 per hour.  Both regimens were given for identical periods of time of 72 hours.  The target dose adjustment was aPTTs in the range of 60 to 100 seconds.
		Aspirin was recommended in all patients at a dose of 325 milligrams a day during hospital stay, but thereafter there was flexibility in the dose of aspirin used.
		The next three or four slides will give you key aspects of both OASIS-1 and 2 that are essentially common.  The patients were entered within 12 hours after the onset of pain.  They were randomized to either treatment for 72 hours.  There was a second randomization in a subgroup of people eligible for the warfarin component that occurred between 12 hours and seven days so this is a partial factorial design.
		Warfarin was then given for three to six months as the standard therapy.  The primary comparison for lepirudin versus heparin in both trials on all endpoints was at seven days and the duration of follow-up in the program as a whole was six months.
		These are the definitions of the various events that were used in OASIS-1 and 2.  They were identical for most events and only different for one event to a small extent based on our experiences in OASIS-1.  
		Cardiovascular death is the same definition that we've used in all trials.  Death was considered to be cardiovascular if it was proven cardiovascular or the cause was unknown, only those deaths that were proven to be non-cardiovascular were called non-cardiovascular.
		New myocardial infarction was defined within the first 24 hours as requiring all three; new clinical symptoms, new enzyme elevation, or ECG changes.  After 24 hours any two out of the three criteria were acceptable, either new clinical symptoms or enzyme changes or ECG changes.
		These are the definitions of refractory angina used in both trials.  Refractory angina was defined very stringently.  Patients had to get typical new chest pain despite optimum medical treatment defined as being on aspirin or another antiplatelet agent and then on at least two anti-anginal treatments, one of which had to be IV nitrates.
		There had to be new ECG changes that indicated ischemia.  In addition to that there had to be an urgent cardiac intervention and it was defined as either thrombolytic therapy for an impending infarction or urgent intervention that is taking the patient rapidly to the cardio cath needing PTCA, CABG surgery or, as I said, thrombolytic therapy, or the insertion of an intra-aortic balloon pump.  Or for those centers where facilities for cardio caths were not available, transfer for intervention in an urgent fashion to one such center.  
		Later on I'll point out to you the overwhelming majority of these patients did, indeed, have an intervention after discharge and before seven days and later as well hospitalizations for angina with ECG changes and admission to an ICU or CCU was accepted also as a criteria.  
		This was double-up because in OASIS-1 there were one or two cases that we noticed and so in a larger study in order to capture these events, the definition was expanded.  Again, the majority of these people had interventions as I'll show you later.
		This is the definition of severe angina.  Severe angina was very similar to refractory angina except that the need for intervention was not there.  It meant again typical chest pain despite medical management, plus new ECG changes.
		I should point out that several trials that have been used as the basis for regulatory approval actually included this definition as refractory angina at least in part.  In a sense the definition of refractory angina in OASIS is stricter, or at least as strict as the strictest there is in the literature.
		These are the baseline characteristics of patients in OASIS-1.  First, the randomization was deliberately unequal in a ratio of four is to three is to three so that 371 patients were randomized to infractionated heparin, 271 to lepirudin low dose, and 267 to the medium dose.
		You will notice from this all of the baseline characteristics are balanced.  About 2/3 were men.  The mean age was 64.  The mean weight was 78.  The majority of people came in with unstable angina.  Only 13 percent were admitted into the trial with an initial diagnosis of myocardial infarction without ST elevation and the majority had abnormal ECGs, and the mean time to randomization was about 6.7 to 7.9 hours.
		These show other key historical aspects.  Again, these are balanced between the three groups.  Myocardial infarction was seen in about 40 percent, previous revasculization procedures in about 30 percent, hypertension in about just under half of the people, 20 percent had diabetes, and 67 percent had a history of previous strokes.  	These baseline characteristics are in general similar to what you would observe in most randomized trials of unstable angina.
		Now, because this was an open trial, we carefully monitored treatments other than the allocated treatments.  You will see the overwhelming majority of patients received aspirin as per the protocol.  The use of nonstudy heparin prior to randomization was similar.  
		The use of nonstudy heparin after randomization was, if anything, lower in the median-dose lepirudin group compared to the unfractionated heparin group with the low dose being in between.  Thrombolytic therapy was used in three percent of those with unfractionated heparin and looks slightly lower in the other two groups.  
		Beta blocker use was 76 percent here, 73 percent in the low dose, and 71 percent in the medium dose.  Nitrate use also showed a trend towards less use in the medium dose.  Calcium channel blocker use was balanced, as was ACE inhibitor use also was balanced.  There is no evidence that the group in the hirudin groups got more aggressive pharmacological therapy that was not part of the protocol mandated regimen.
		These are the data on aPTT over the first 72 to 96 hours.  The blue is unfractionated heparin and because of the bolus, and as described in numerous studies, you get an initially higher level with heparin than with the hirudins.  Orange is the low dose and the yellow is the medium dose of hirudin.  And you can see that these two doses, the medium dose and the unfractionated heparin, for what it's worth had a similar aPTT, whereas the low dose had a slightly lower aPTT.
		These are the main efficacy results of OASIS-1.  The composite of cardiovascular death, myocardial infarction, refractory angina, as well as severe angina which is the main endpoint, showed a dose dependent reduction so that it was 15.6 percent in the unfractionated heparin group, 12.5 percent in the low dose group, and 9.4 percent in the medium dose hirudin group.  The difference between this and this is statistically significant.  A test for trend is also statistically significant.
		The same results were obtained for cardiovascular death, myocardial infarction, and refractory angina.  You will see 6.5 percent, 4.4 percent, and 3.0 percent.  The difference between unfractionated heparin and the medium dose is nominally significant.  	Again, a trend towards lower rates for cardiovascular death and myocardial infarction was also observed compared to unfractionated heparin.
		The next slide indicates that during the treatment period we would have expected almost all or the majority of benefit to emerge.  Indeed, that was the case.  You will see the differences in the quadruple endpoint.  In the triple endpoint, and on cardiovascular death and MI trends emerge entirely during the treatment period with little further benefit beyond that.
		The next slide shows you the components of these and this on cardiovascular deaths represents very few events, one or two per group.  When you look at more frequent events, myocardial infarction is a dose dependent relationship.  Refractory angina, at least for the medium dose, there is a reduction.  And for sever angina there is a dose dependent relationship.  At least these three components contribute to the differences in the composite outcome.
		These are the data on long-term follow up.  You will see for the three sets of composite endpoints the early differences between heparin and the two doses of hirudin persist in general up to six months and you will see that for the composite refractory, and you'll see that for the composite with cavuvast cadet and myocardial infarction.  There is new evidence that after three days of therapy the --
		(Whereupon, off the record when the recording stopped and information was lost.  Back on the record at 9:56 a.m.)
		DR. PACKER:  This would be a good time to open the discussion of OASIS-1.  Open for discussion.  We'll begin with our primary reviewer, Dr. Borer.
		DR. BORER:  Salim, I have several methodological questions that probably are easy to deal with that weren't clear to me from the book that we were given, not in any particular order.
		How was the patient variation and response to warfarin resolved, or was it?  As I understood the protocol, everybody got 10 milligrams initially by mouth and then three milligrams a day and there was no monitoring of pro time or INR to titrate the dose.  First, am I correct in that?
		DR. YUSUF:  There was monitoring.  First, let me tell you in OASIS-1 nobody was randomized before three days because there was concern on bleeding or putting a new drug and warfarin together.  The mean time to randomization was about six or seven days so it was well after the hirudin was given.
		The second is there was monitoring of INRs frequently.  I think it was daily for the first three days and then less frequently.  I don't remember the exact regimen but it was done.
		DR. BORER:  Was the dose then varied in response to the INR?
		DR. YUSUF:  Yes, the dose was then varied.
		DR. BORER:  I see.  Okay.  That wasn't clear to me.  The severe angina and refractory angina endpoints are based on a case report form?
		DR. YUSUF:  Yes.  Also one other thing.  Each of the things we were interested was documented.  We asked for all the ECGs.  They were read centrally.  We asked for the discharge summary and they were also looked at.
 		DR. BORER:  Okay.  My recollection reading through the reports of OASIS-1 and OASIS-2 was that at least in OASIS-2, which I'm not asking about now, there was the potential for missing the angina events in patients who didn't have a completed seven-day report because the forms then would only capture mortality and myocardial infarction.  Was this true also in OASIS-1?  Was there potential for missing the angina events in people who did not have completed form at seven days or seven-day complete reports and did that happen?  I mean, were there incomplete reports?
		DR. YUSUF:  I think there were about -- actually, at seven days we had complete follow-up in OASIS-1 in all the patients.  I have a backup slide but it shows we have complete data at seven days in everybody.  In OASIS-2 we have missing data on seven in each group.  That is 14 out of 10,000 people for that outcome.
		DR. BORER:  Okay.  We'll get to OASIS-2 later but I was more concerned about OASIS-1 now.  After the initial period of hospitalization, aspirin dose was variable.  Did you make any effort to analyze the follow-up data based on aspirin dose?  Was aspirin a confound or do we not know?
		DR. YUSUF:  After seven days we didn't try to do that.  Before seven days, as you can see, almost everybody got it so you couldn't do a stratified analysis.
		DR. BORER:  The Inclusion of patient into the warfarin follow-on, that did not include the entire population, did it?  You know, we can talk all day about biases and such but I would like to hear just what you have to say about the potential for selection bias that might have confounded OASIS-1 based on the use or non-use of warfarin.
		DR. YUSUF:  I think the first thing was not everybody was eligible for warfarin.  For instance, if they had bleeding on hirudin, physicians would give -- or heparin, physicians would be reluctant to use it.  
		Second thing we found given that OASIS-1 was done in North America was that there was a considerable reluctance on the part of physicians to randomize people to warfarin so that only about 35 or 40 percent eventually got randomized.  Now, the people who got randomized turned out to be a lower risk group than the people who didn't.  
		People who had refractory angina and had an intervention, the physicians thought they had fixed all the problems so they never got randomized to that.  In the end from a trial point of view, the warfarin part did not help us because we weren't able to answer the warfarin question and what we learned is physicians don't like using warfarin.  
		The key thing is warfarin was started around five to six days in OASIS-1.  By the time you get an effective INR, it's beyond the seven days so it's unlikely to have any effect.  We've also done stratified analysis so it was balanced.  The few people who got into the study was balanced by the three randomizations and the results stratified or adjusted did not make much difference to the results.
		DR. BORER:  What was non-study heparin in the heparin group?
		DR. YUSUF:  Non-study heparin was if at any stage -- okay, there were two.  First, before getting into the trial some patients could have been in heparin and then when they get randomized, they go to the randomized therapy so that's one.
		The second is at the end of 72 hours some physicians wanted to continue heparin longer, given antithrombotic therapy longer so then when we stopped it, they used it for a longer period of time, usually a couple of days more.
		DR. BORER:  Did you make any effort to analyze the results based on whether non-study heparin was added on or not?
		DR. YUSUF:  As I showed you, it was added on less in the medium dose hirudin.
		DR. BORER:  One final question that I have.  You indicated -- and this is just so I can get clear here.  I'm not making a qualitative statement.  You indicated that the main endpoint was the quadruple endpoint.  That's what you were looking at at seven days.  Is that something that was determined before the study or is that something that was determined after the results were in?
		DR. YUSUF:  Well, what happened, I mean, is as follows.  We did not clearly expect in a 900 patient study divided three ways to get overwhelming results so we said here are the three composites.  We have high power on this composite and we said these are the three endpoints that we're interested in.  
		We knew we had very low power on cardiovascular death and MI.  We had some power on refractory angina.  For the one endpoint that we calculated was the first one.  We didn't say one is primary, one is secondary, and one is tersary.  Implicitly, that was the order in which one assumed it would be the case.
		DR. BORER:  Thank you.
		DR. KONSTAM:  Can I follow up on that?
		DR. PACKER:  Yeah, Marv.  Go ahead.
		DR. KONSTAM:  I'm still not sure.  Let's start with the severe angina endpoint.  That was specified in the protocol as something you were going to look at?
		DR. YUSUF:  Absolutely.
		DR. KONSTAM:  And when you say that -- you mentioned that the selection or endpoint retrospectively might be rationalized on the basis of the way you performed the power analysis.  What was the power analysis exactly performed on?
		DR. YUSUF:  It was performed on the quadruple.
		DR. KONSTAM:  It was specified in the protocol that the power analysis was done on the quadruple?
		DR. YUSUF:  Yes.
		DR. KONSTAM:  At seven days?
		DR. YUSUF:  At seven days.
		DR. KONSTAM:  That's also --
		DR. YUSUF:  It's in the protocol.
		DR. PACKER:  Ileana and then John.
		DR. PIÑA:  Salim, how many patients were actually on heparin at the time of their admission before the randomization occurred?  I would assume that some patients came in with chest pain and they were automatically put on heparin.  Was there any adjustment time stopping the heparin and starting the randomization drug?  How was that handled?
		DR. YUSUF:  I think about approximately 29 or 30 percent, if I'm remembering the slide, were on heparin before they got into the study and the instructions that we gave people is as soon as you get the telephone randomized allocation, switch to the study medications.
		DR. PIÑA:  So just make a change?
		DR. YUSUF:  Yes.  And we did document that it did happen.  Obviously there may be a five or 10-minute delay but it happened very rapidly.
		DR. PIÑA:  And that includes the bolus?
		DR. YUSUF:  Yes.  Well, okay.  That's a good question.  If you were on previous heparin, the bolus was skipped.
		DR. PIÑA:  Do you think that could have affected that early increase in PTT that you saw with the heparin group on the graph?
		DR. YUSUF:  Well, if you were on heparin, the bolus was skipped so that wouldn't account for it but it's the other people that you get that so the remaining 2/3 is where you get that peak.  You're right, Ileana.
		DR. PIÑA:  Did you collect aPTTs in the group on heparin before they were randomized?  In other words, you knew where they were before they got randomized?
		DR. YUSUF:  Yes.  It was a requirement of the protocol.
		DR. PIÑA:  Another one of my confusions is the severe angina, refractory angina, because it sounds like the different is really a matter of the physician judgment at some point where intervention is required.
		DR. YUSUF:  That's right.
		DR. PIÑA:  Do you have a sense of how many patients were initially classified as severe angina that went on to become refractory?  In other words, they had the intervention?  When did you capture that or did you capture that?
		DR. YUSUF:  We captured it but for this analysis that I'm presenting to you, the most severe first event is what's counted.  No, that's not true.  		The first event is what's counted within seven days, but then for the triple endpoint the most severe is counted so for the quadruple endpoint if severe angina occurred and then somebody had refractory angina and the same patient had an MI and then died, in the analysis you take the first one.  For the triple endpoint you don't worry about severe angina and for the double endpoint you don't worry about a minor event unless there were clinical important events that occurred earlier.
		DR. PIÑA:  One last question.  When you randomized after the seven days either to warfarin or standard, what was standard?
		DR. YUSUF:  Standard was everybody received aspirin so standard was no treatment.  Ho warfarin.
		DR. PIÑA:  Aspirin and nothing else?
		DR. YUSUF:  Yes.  Well, beta blockers.
		DR. PIÑA:  Oh, yeah.  The additional medication but not anticoagulant.
		DR. YUSUF:  Sure.
		DR. PACKER:  John. 
		DR. DIMARCO:  Salim, patients were randomized in the emergency room.  Is that correct?
		DR. YUSUF:  Sometimes in the CCU.
		DR. DIMARCO:  Okay.  Wherever the event occurred.  Were they pain free at the time of randomization?
		DR. YUSUF:  Some were and I think, what is it, 60 percent had pain.  We have the data and we've looked at it.  It was approximately half had pain and half did not have pain at the time of randomization with a plus of 10 percent.
		DR. DIMARCO:  What I'm curious about is in the patients who, you know, you have 10, 12, 13 percent who have MI without ST segment elevation and one of your endpoints is new MI, how did you distinguish between those two?  Did the pain have to go away and then they had some pain free interval and then they had recurrent pain?
		DR. YUSUF:  New ECG changes and new enzyme elevation.
		DR. DIMARCO:  Well, the enzymes would have still been up from the first -- 
		DR. YUSUF:  Yes.  The first 24 hours, John, is very complex to diagnose.  I agree with you.  That was a challenge to do that.
		DR. DIMARCO:  I'm just curious how you did it exactly.
		DR. YUSUF:  First they needed new pain in the first 24 hours.
		DR. DIMARCO:  So the pain had to go away?
		DR. YUSUF:  Had to go away and you needed new pain and it was meant to be more than 20 minutes.  Not just a little bit of pain requiring nitro but more than 20 minutes.  Then they needed new ECG changes.  Then you needed further elevation in the enzyme which is if it was already elevated, a further 20 percent increase.
		Then a committee looked at all of this blindly.  The majority of new MIs did not occur after the first day.  You could see that from the curves that I showed you.
 		DR. PACKER:  Tom Graboys.
		DR. GRABOYS:  Just to follow up on that, were you able to obtain triponen levels on any of these patients?
		DR. YUSUF:  At the time we did the study, triponen was not commonly available in Canada.  In fact, I don't think any of us had triponen.  We talked about it.
		DR. PACKER:  Rob Califf.
		DR. CALIFF:  There are a lot of interesting things about this presentation and I know they will keep coming up again and again.  First of all, just in terms of discussion within the committee, I think that the way you've handled this is about as well as it can be done.  Issues in the first 24 hours are almost impossible to sort out.  
		I would point out that this is a population without ST elevation so they typically don't have six or eight hours of pain.  That would be highly unusual so the recurrent pain is a little easier here than it is in an ST elevation population where frequently the discomfort won't go away for eight, 10, 12 hours.  
		The enzymes are almost impossible because if they are up to start with in the first 24 hours, trying to really sort that out is difficult so we are probably missing a lot of recurrent events in the first 24 hours just because you don't have a clean way of sorting it out, nor will triponen be helpful because once it's up, it's up for a long time.  There are some really complicated and difficult issues here.
		One of the things about what you've done here is proposing to combine OASIS-1 and OASIS-2.  I know we're going to get into more.
		DR. PACKER:  Right.  We're going to get into this.
		DR. CALIFF:  So hold off on that?   
		DR. PACKER:  Hold off on that.
		DR. CALIFF:  All right.  Then I'll go to my last point which is the refractory angina definition.  I'm not aware of a plain way to do this because any way you look at it, it's pretty subjective.  In terms of what you did with the sites, did you only look at cases where the sites called it an event and then you adjudicated it?  Or did you go back and actually review every record for things that might have told you there was an event that the site wasn't picking up?  If you did the latter, how did you really go about that?
		DR. YUSUF:  We did both.  We obviously took the events reported and then we adjudicated it centrally.  In 45 percent of the patients across all sites a monitor was sent out to scan the charts to see if there were any events missed.  It wasn't done 100 percent.  I was done in approximately half the people.
		DR. CALIFF:  What did you find in that 45 percent?  Were the sites missing events?
		DR. YUSUF:  The company did it so they know the answers to that.
		DR. LUZ:  There were no previously unreported events of death, MI, or refractory angina.  There were a total of four severe angina events, three of which occurred before day seven, two in the heparin group, one in the low dose lepirudin group, and one additional severe angina event up to 35 days that was considered in the medium dose lepirudin group.
		DR. YUSUF:  At seven days it is 410.  Is that right, the missed event?  210 severe angina.
		DR. CALIFF:  Just to clarify, this is OASIS-1 that we're talking about?
		DR. YUSUF:  OASIS-1.
		DR. CALIFF:  That seems almost too good.  I've never seen monitoring that would pick up so few differences with a site.
		DR. YUSUF:  I don't know.
		DR. LUZ:  In addition, one should perhaps mention that the FDA has inspected one of the OASIS-1 clinical sites and did not detect any previously unreported events during the hospital phase.
		DR. PACKER:  But this is worth asking about because in every trial that this committee has seen, including trials that are double-blind, the audit process picks up a higher frequency of discrepancies, routinely picks it up.  
		It's just part of the expected process of looking at the difference between what is reported on the case report form and what actually may or may not occur at a site.  Can you describe the audit procedure that was followed in OASIS-1?
		DR. CALIFF:  Nothing I feel compelled to add.  I mean, our work which shows if you had two clinicians looking at the same patient at the same time, you wouldn't have agreement that was quite this high.  This is difficult but I think it would be worthwhile to go through it.
		DR. YUSUF:  I mean, I've told you what I now, Milton.  I think there is one thing, though.  Our definitions and our forms match identically which is important.  Our definitions are pretty stringent.  I know severe angina is the least stringent of the three but you can always pick up interventions if you carefully chart it.  
		Since the need for intervention is a key part of refractory angina, I doubt that we truly missed refractory anginas because of the audit.  And with MIs, too, we had very clear definitions and people had to meet them.
		The other thing is we asked them to send us every enzyme value in every patient centrally so sometimes if a center said this is not an MI and scanning it centrally we found an enzyme pattern that was typical, we went back centrally and asked them, "Are you sure this is not an MI?  Send us the case charts."  And we scanned that.  
		In a sense, what you would normally do at a site audit we did it by fax centrally because of the way we managed the trial.
		DR. CALIFF:  I think the key thing here is a requirement for intervention was part of the definition.   
		DR. PACKER:  But not for severe.
		DR. CALIFF:  For refractory but not for severe.  Right.
		DR. PACKER:  But I'm still confused.  We're dealing with a putative primary endpoint that is driven primarily by severe.  That constitutes most of that endpoint.
		DR. YUSUF:  That's partly true, Milton, but also when you look at the composite with refractory angina without severe angina, you get the same dose dependent relationship and the difference between unfractionated heparin and medium dose heparin is -- medium dose hirudin is nominally significant.  It's a consistency.
		DR. PACKER:  I understand but we're still -- I'm still confused by this.  It is a true statement that most of the endpoint that includes severe angina is driven by the episodes of severe angina.
		DR. ARMSTRONG:  It looks like it's about half, Milton.
		DR. PACKER:  About half.  Right.  But the delta is driven primarily by the delta on that component.
		DR. ARMSTRONG:  About half.
		DR. YUSUF:  On that endpoint, yes.  But if you take the CV death MI refractory angina, it's really driven by both MI and the interventions.
		DR. GRABOYS:  The delta is 23.
		DR. YUSUF:  I'm sorry, Tom?
		DR. GRABOYS:  At day seven the delta is 23 when you include severe angina, 16 when you don't, and when you just look at death MI it's 11.
		DR. YUSUF:  Okay.  So they both contribute to it.
		DR. PACKER:  Can you tell us more about the audit and what was done and how it was carried out?
		DR. LUZ:  What was actually done was that in the patients that were randomly selected, the case record form was 100 percent verified meaning that each and every entry made into the case record form was reconciled with the medical charts.  In addition, the medical charts were screened to see whether there were any additional entries that were not captured by the case record form.  
		One point that you might want to be aware of, we're talking about a study of only 900 patients and a relatively small overall number of events.  The four severe angina events are, in fact, a certain percentage.  One certainly has to put this into perspective with the overall number of events and that it's maybe not this surprisingly low.
		DR. PACKER:  When you say the charts were screened for events, the patient's record, charts were screened for events, what -- and the criteria that were used by the auditors were the criteria, the definitions, that you showed us today?
		DR. LUZ:  Essentially, yes.  Of course, the monitors were not medical doctors that were able to really make an assessment whether this is refractory, severe, or recurring angina.  What they were looking for was each and every event that was marked to be ischemia or whether there was an ECG indicative of ischemic changes.
		DR. PACKER:  And that these were monitors that were employees of Aventis?
		DR. LUZ:  Yes.
		DR. PACKER:  And they were unblinded?
		DR. LUZ:  Well, they were as unblinded as the trial was.
		DR. PACKER:  This is an unblinded audit?
		DR. LUZ:  The trial was unblinded with respect to the comparison of heparin versus lepirudin and it was blinded within the lepirudin doses and the audits were done exactly the same way.
		DR. PACKER:  I'm just wondering.
		DR. YUSUF:  Can I make a --
		DR. PACKER:  Salim, I'm just wondering how much comfort we can take from an audit carried out by a sponsored where the auditor knew the identify of the treatment.
		DR. YUSUF:  Can I make two points?  The audit consisted of really two parts.  One part is every single enzyme value in every patient had to be sent to us documented in the form and then that was reviewed without knowing the allocation.  That is unbiased.
		The second thing was the -- there are two other events they are looking for.  I agree that severe angina could well be a little soft when somebody is looking at it at the center.  The second part is refractory angina needed an intervention and that is a hard one to be biased on.  It's a pretty hard one.  
		All the enzymes, B at the CCC reviewed blindly.  MIs we would have definitely picked up.  I believe the refractory anginas we picked up.  I agree severe angina, that question that you raised, we'll have to think about.
		DR. PACKER:  I think it would be hard to feel reassured here that we're having a treatment effect on a putative endpoint driven by severe angina which is the most subject to interpretation in an unblinded trial where the investigator knows who's getting what, audited by company employees who are aware of the treatment assigned.  I'm not reassured.
		DR. CALIFF:  Milt, you certainly pointed out the flaws in a phase to experience which was designed, I think, to understand what an appropriate dose would be to take into Phase III.  We're not cynical enough to believe that -- I just want to say this.  
		We're not cynical enough to believe that most investigators would alter the results or somehow in a cynical way try to make the treatment look better than it really is.  It's just not as good a methodology as a blinded study.  We're also not saying that company employees would alter records typically.  Are we?		
		DR. PACKER:  I'm just saying that you generally find what you look for.
		DR. CALIFF:  So the bias is not easy to quantify.  I think you would agree with that.  Wouldn't you, Salim?
		DR. YUSUF:  Well, I think on CV death MI and refractory angina it's very unlikely there was material bias.  I agree with Milton that there is a certain concern of potential bias on the severe angina component.  I hope most people think that is a reasonable position.
		DR. PACKER:  I wanted to ask one issue --
 		DR. FLEMING:  Before leaving this point, just to quickly comment, Rob, the issue could certainly, though, be that chances or subconscious views of what the profile would be of a known intervention could influence decisions for when you would perform other interventions.  So in a trial where the physician judgment influences the occurrence of the endpoint, the lack of blinding could, in fact, enter in.
		DR. CALIFF:  And it could work either way, though.  Couldn't it?  For example, if the nurse was really scared about this new experimental treatment and knew the patient was getting it, the patient might be watched more carefully.
		DR. PACKER:  I wanted to ask Tom to pursue this but let me see if I understand correctly and just for clarification purposes before turning it over to Dr. Fleming.  There was no prespecified primary endpoint in this study.  Is that correct?
		DR. YUSUF:  We did not put the word primary against any of the three endpoints.  As I said, there was one endpoint on which we calculated our calculation.
		DR. PACKER:  I just want to make a -- endpoint that you calculate power is not necessarily the endpoint that one spends alpha on.  One has all sorts of opportunities to power on endpoints which are not the primary endpoint.  It's actually occurring to an increasing degree.
		I'm trying to figure out that you had in the absence of a prespecified primary endpoint and in the absence of a statistical plan, one had three possible endpoints examined at three different times across three different treatments.  How does one know what is the critical p-value to examine any of these endpoints?
		DR. YUSUF:  I think a point to note is there were only three endpoints and they were all specified to be looked at one time point.  The others were consistency analysis.  The long term was consistency to see you don't lose the benefit.  The early one was to see when does the benefit emerge.  		Really there were three analyses and I think in this context we are looking at three that are concordant.  All three that are concordant.  There is really no statistical way to analyze what three events that are highly correlated and they are concordant.  It is reassuring that for all three endpoints the pattern of the results is identical.
		DR. PACKER:  Tom, any questions?
		DR. FLEMING:  No.
		DR. PACKER:  I'm sorry, Joann.
		DR. LINDENFELD:  That's okay.  The creatinine cut off for OASIS-1 was 2?  Is that correct?
		DR. YUSUF:  Can you help me, Matthias?  Was that right?
		DR. LINDENFELD:  I guess in follow-up to that, I wonder if we could see what the average creatinine was or how many there were that were 1.5 to 2.
		DR. YUSUF:  It's about 97 if I remember.  You know what I mean.
		DR. LINDENFELD:  Right.  The point I'm getting at here is we're going to come --
		DR. YUSUF:  We don't know that now, Joann.
		DR. LINDENFELD:  We're going to come back to this problem of how to use the drug with renal insufficiency and I think we're going to need to know that for both studies and to just maybe look at the patients in that upper creatinine range if we have any.
		DR. LUZ:  We can use the analogy with OASIS-2.  Both studies specified in the protocols that patients would have to be excluded from participation if they had know renal insufficiency as assessed by creatinine level of 2.0.  The creatinine level was not required to be available at the time of randomization.  In OASIS-2 we had about five percent of all patients that had a level that was higher than 1.5.  Very few that had more than 2.0
		DR. YUSUF:  And I think, Matthias -- sorry, Joann.  Matthias will show you data, at least from OASIS-2 by creatinine.
		DR. LINDENFELD:  Okay.  Good.  A second question I have is about pro times for INRs.  The published paper says the warfarin was started within 12 to 24 hours but it was actually started later.  Is that right?
		DR. YUSUF:  Yes.  There were two phases.  One was where it was started well after the infusion because the company was concerned.
		DR. LINDENFELD:  In the publication it says in Phase II it was started 12 to 24 hours after treatment.
		DR. YUSUF:  After treatment.  So after three days?
		DR. LINDENFELD:  After three days.  And do you have INRs?  I recognize that --
		DR. YUSUF:  Yes.
		DR. LINDENFELD:  Between the two treatment groups?
		DR. YUSUF:  The target INR was in the first trial 1.5 to 2, very low INRs.  In the second trial 2 to 2.5.  Now, I don't remember what was achieved by seven days but the vast majority was subtheraputic.  That was one of the problems we found because, remember, you started on day three to day four and by seven days the vast majority we weren't dosing.
		DR. LINDENFELD:  I just wondered if there was any difference between the two groups, heparin versus --
		DR. YUSUF:  No, there wasn't.
		DR. PACKER:  Paul.
		DR. ARMSTRONG:  Salim, our briefing notes suggest that severe angina was added in Phase B and not present in Phase A so I presume there was a protocol modification.  They also suggest that the definition was two episodes of recurrent angina as opposed to one of which one required ST segment change.  Can you just clarify that for me?
		DR. YUSUF:  Matthias, can you clarify?  You're right, Paul, there were some changes between the first phase and the second phase.
		DR. LUZ:  You're right with both points.  Severe angina was introduced before the second part of the OASIS-1 study took off and was actually introduced by the investigators group before knowing the exact results.
		DR. YUSUF:  And, in fact, well before then.
		DR. ARMSTRONG:  So the planning must initially have occurred without recurrent or what you call severe angina as part of the analysis plan and then that analysis plan must have been modified when that diagnosis was incorporated in Phase B.  Then how was that diagnosis established in retrospect in Phase A?
		DR. LUZ:  All patients who had recurrent angina were reajudicated by the blinded adjudication committee again.
		DR. YUSUF:  And all the recurrent anginas, which is a broader basket, were reported and we had required them to fill out whether there were ECG changes, recorded all the enzymes and the interventions so the committee was able to do it.
		DR. ARMSTRONG:  My second question is to further explore the issue of MI in the first 24 hours.  As I understand it. it was either/or on enzymes or ECG changes in association with what was perceived by the investigator to be clinical symptoms.  Can you clarify for me what the ECG definition of an MI was as opposed to refractory ischemia in that similar time point and what component of the MIs were established by an ECG criteria alone?
		DR. YUSUF:  The ECG criteria in the first 24 hours required ST elevation or persistent ST depression of more than 2 milliliters which wasn't there previously along with the symptoms.  My recollection, and these analyses could be done but I don't have it right now.  
		My recollection is the majority of events that the adjudication committee classified were pain plus ECG because despite the fact we had enzymes for the first 24 hours.  Just like Rob said, it was hard to interpret.  I was not involved deliberately in the adjudication committee.  It was run by Cam Joiner totally independent of Hamilton.
		DR. ARMSTRONG:  So the new ECG changes for refractory ischemia by contrast would be characterized as what?
		DR. YUSUF:  ST depression, ulteen version, or transient ST elevations.
		DR. ARMSTRONG:  And, finally, 13 percent of the patients had an MI on admission as their qualifying event which would be substantially lower than a number of other large trials of a similar syndrome.  Any comments in relationship to that frequency which is often 45 percent of the population?
		DR. YUSUF:  I don't know, Paul.  Obviously it depends on the trial you look at.  I mean, some trials like the GUSTO trial, you're right, had more people but I think there was an attempt to have so many people with MI without ST elevation.  
		We had no such attempt.  We also did a large registry, as you know, and this is approximately in that ballpark.  Right now we are running CURE and this isn't the same ballpark.  I think it may be the way we've defined the entry criteria.
		DR. ARMSTRONG:  Thank you.
		DR. PACKER:  Marv.  
		DR. KONSTAM:  Salim, there were three treatment groups, right?  How many comparisons across those three groups were you intending to make?
		DR. YUSUF:  Well, we were really intending a dose-dependent analysis to look at whether there were trends.  And we were intending to look at the extremes versus the -- you know, the two extremes.
		DR. KONSTAM:  Well, I mean, the p-values that you showed us.  For example, for the quadruple endpoint, I see a p-value of .018.  What is that p-value?
		DR. YUSUF:  This is between the two.
		DR. KONSTAM:  Right.  So this is between two of the groups.  This is between the heparin and the high dose.
		DR. YUSUF:  And if you do one for trend, it's also significant.  I don't remember the exact p-value.  If you do an analysis of variance, it is significant.  Then you go to the next step of finding out where the p-value comes from.  It's like a second step procedure.
		DR. KONSTAM:  No, but the .018 is just --
		DR. YUSUF:  The extremes.  
		DR. KONSTAM:  I mean, would you suggest there ought to be a correction of that given the fact that you are also comparing the low dose to heparin?
		DR. YUSUF:  There are problems in trying to do a correction and here is the way.  The first analysis when you have three doses is you look for trends.  Once that is significant then you are exploring where that p-value for trend comes from so it's like a dependent analysis.  I know where you're getting at.  This is not sort of doing multiple analyses and then choosing the best p-value.
		DR. KONSTAM:  Maybe Tom will comment.  I think the problem that we're going to have in trying to use this study as support for OASIS-2, one of the problems is we have multiple endpoints, multiple time points without really clear prespecification of a primary endpoint or time point in the protocol.  Then we have three groups so there's lots of p-values.  I guess, you know, it would be helpful to sort of get some feeling for how meaningful any one p-value is.
		DR. FLEMING:  Just to briefly comment, there are many issues and I'm awaiting the presentation of OASIS-2 before getting into them because it will be easier to address them globally but just one brief comment.  
		This analysis, as I understand, this choice of this endpoint wasn't based on a predetermined idea that this was the most clinically relevant.  Salim has already pointed out this is the endpoint that was going to have the most events and it gave you in a small screening trial at least some opportunity to have power on something.  
		This isn't even an endpoint that's in the labeling indication so there is a paradox right there in terms of is it important and is it significant or not.  I guess I'm not worried in determining whether it's significant or not because there are so many other issues that are limiting the convincingness of this result in the total context of what we have.
		DR. KOCH:  Gary Koch, University of North Carolina.  As was stated before, there was no formal analysis plan so all that one can do is to talk about what hypothetically might have been done.  In a study of this type normally you would test the high dose against placebo first which would be the medium versus placebo.  That's a comparison that is emphasized.  
		If that's significant, you then step down to the lower dose versus placebo.  The other method sometimes used is called the Hawkberg Method for multiple comparisons.  With that method if both doses beat placebo with p less than 05, you get both doses.  Otherwise, you test the dose with a stronger p-value at 025.  
		On the four-way endpoint you could say from a post hoc hypothetical perspective it would meet it.  You could also say the study was powered for the four-way endpoint.  You get a favorable result for the four-way endpoint, you step down to the three-way endpoint taking away the severes.  You get a good result on that, you take away the refractories and step down to the other.  
		Hypothetically one could have said that had a rigorous analysis plan been written for this study, it might have emphasized the p-values that were shown.  No such plan was written and so you just have to interpret these as a way of looking at the data and weight them as you consider appropriate.
		DR. YUSUF:  I think Tom's comment is appropriate.  This is a study that was really designed to help us go to the next step and we have these results and these p-values and, as you know, we didn't decide at that stage to claim victory.  We wanted more data.
		DR. CALIFF:  But just to -- I mean, Gary stated the typical way it might be done but it's also true, isn't it, that depending on what you believe ahead of time, you could design an analysis strategy for the same problem that might emphasize one or another comparison and segment the total.
		DR. YUSUF:  I can tell you what we did.  You're right.  There wasn't a preanalysis plan but we did a thing for a three-way analysis which you do.  That's the basis statistics.  I've learned when you have three groups you test that across the three groups.  Once that's significant, then you explore where the significance comes from.  Maybe a more elementary approach.  		One little clarification.  There is only one time point that was really specified when we do that.  
		DR. CALIFF:  Another point I wanted to make was what Dr. Koch described might be the most often used approach but one could, for example, put all your emphasis on the high dose comparison.  It's hard to know unless it was written down.
		DR. KOCH:  That's what I said in this particular case.  If a plan would have been written, it would have put all the emphasis either on a trend test or on the comparison of the medium dose versus placebo both of which are identical in this case.
		In this study that is all the more likely hypothetically because a high dose was considered and then was abandoned before the study was implemented.  		One could say hypothetically that if there was a dose that the investigators believed was going to have the most action, it was going to be the medium dose.  Again, all of this is hypothetical.
		DR. YUSUF:  I think the key thing is that the aim of this part of the study, Milton, was to help us design the next study.
		DR. PACKER:  I just want to make sure that we have adequate clarification on Paul's comment.  Has an analysis been done on the -- I think you stated, Salim, that the original sample size of OASIS-1A and 1B combined was based on the quadruple endpoint, the quadruple endpoint, however, being recurrent and not severe angina.  Has an analysis been done of the endpoint that you stated was the original endpoint for a basis of power calculations?
		DR. YUSUF:  Milton, in an ideal world we would like to think that trials are sort of designed as so much power and then so much endpoint.  In this case what happened is we were allowed to only study so many people so we then backed up and said this is what power we had in this endpoint.  
		The recurrent angina part of it we found was a mish mash of so many events that we could not get objective documentation.  We recognize that in the first 50 to 100 patients.  We said recurrent angina is something we can't place much emphasis on.  So at that stage we always knew we would go for 900.  Then we looked at this and said if we had severe angina with these event rates, this is what our power would be.
		But, Salim, in all fairness, and I don't want to belabor this issue, we can all appreciate very much that you only had 900 patients and that was fine but it's a difference to say that you had a chance to only study 900 patients compared with the statement that there was a prespecified quadruple endpoint defined in a specific way in the original protocol that was the basis of the claim that that was the primary endpoint.
		DR. YUSUF:  That wasn't stated in the protocol that recurrent angina is a quadruple.  Is that right, Matthias?
		DR. LUZ:  Yes.
		DR. YUSUF:  No, it wasn't stated the way 
-- I may have given you the wrong impression.  Recurrent angina was not stated as a primary endpoint.
		DR. PACKER:  According to the FDA review, the clinical markers were a recurrent angina refractory, angina subsequent MI and cardiovascular death.
		DR. YUSUF:  All four were collected as was also collected in OASIS-2.  They were collected.  Four endpoints were collected.
		DR. PACKER:  Okay.  I think we've beaten this to death.  Why don't we go on to OASIS-2.
		DR. YUSUF:  Okay.  Can I have the next slide and have a minute to breathe.  The next two parts of the presentation will be on the results of OASIS-2.  Then the third part is an analysis showing you the consistency of results between OASIS-1 and 2.
		The OASIS-2 patient population was identical to that in OASIS-1.  In contrast to OASIS-1 two things were done.  First, it was a double-blind study, and, second, we only focus on medium dose lepirudin versus the active control of unfractionated heparin.
		10,141 patients were randomized.  The primary endpoint was cardiovascular death or new myocardial infarction at seven days.  Only one key secondary endpoint was identified.  There were others identified but they were called other endpoints so the key secondary endpoint was the composite of cardiovascular death, new myocardial infarction or refractory angina at seven days which we've discussed for OASIS-1 and which was nominally significant there.
		Other endpoints were the double and the triple endpoints, that is, these two endpoints, at the end of 72 hours which was the end of treatment.  The point of doing this was to look at biological coherence and see if the results emerge during treatment.
		Then it was also done at 35 days to see if we had lost the treatment benefit.  Revascularization procedures by seven days was also one of the three specified endpoints.  Adjudication was again central and blinded.
		There were the par calculations.  Based on OASIS-1 and a large registry that we were running, we anticipated at seven days an event rate of 5.5 percent in the heparin group.  If we observe this, then we would have 90 percent power to show a 25 percent risk reduction compared to heparin, or 80 percent power to show a 22 percent risk reduction.
		We also did par calculations for slightly higher event rates and slightly lower event rates and we were comforted that if we got an event rate of five percent, we still had a reasonable trial.
		For the second re-endpoint again, par calculations were made at 8.7 percent for the composite.  These were the relative risk reductions that would be detected at an alpha value of 0.01.
		However, we observed a lower cardiovascular death and new MI rate of only 4.2 percent compared to 5.5 percent, almost 20 percent lower for the primary endpoint and also for the second re-endpoint it was 6.7 percent which is 8.7 percent.  This seriously compromised the power of the study.
		These were the regimens.  The lepirudin dose was identical to the medium dose used in OASIS-1.  Unfractionated heparin was very similar and, as Matthias Luz pointed out, instead of a fixed infusion rate per hour, it was slightly modified to be a weight adjusted dose but the mean dose happened to be very close to what was used in OASIS-1.
		The same aPTT was started and the same recommendations for aspirin and, as before, the majority of patients received an anti-platelet drug.
		The first trial was entirely done in Canada.  This trial was a global study with patients from North America, Western Europe, South Africa, Australia and Israel, South America, and Eastern Europe representing a broad range of clinical practices.
		Again, the baseline characteristics are similar between the two randomized groups.  As before, about 60 percent were men, mean age was 64, unstable angina was about 88 percent, almost identical to the first study.  Abnormal CG was seen in 90 percent and the mean time from pain to onset of randomization was just over six hours.
		These are the data on key historical aspects and, like before, about 40 percent had a previous MI.  The proportion of people who had a previous revascularization procedure was slightly lower than the first study which was entirely done in North America.  All other factors were very similar.  About half were hypertensives, about 20 percent were diabetics, and about four percent had previous strokes.
		These are the data on aPTT.  As before in OASIS-1 during the first 12 hours the aPTT values were higher with unfractionated heparin and then lepirudin caught up and then they were both within the established range of 60 to 100 seconds during the rest of the infusion period.
		These are the primary efficacy analysis.  The primary endpoint was cardiovascular death and myocardial infarction at seven days.  There was a 16 percent risk reduction which was a p of 0.086 which is short of our prespecified 0.05 but came close.
		A second re-endpoint was cardiovascular death, myocardial infarction, and refractory angina prespecified at seven days and there was an 18 percent risk reduction that is nominally significant and came very close to a prespecified 0.01.
		These are the data to look at internal biological coherence which is again prespecified in the analysis plan so that at the end of 72 hours the entire difference between the two groups emerged so there is a 24 percent risk reduction at the end of treatment which is nominally significant.  On the triple endpoint there's a 22 percent risk reduction that is nominally significant and you can see these two results are approximately the same in relative risk reduction.  That was also true of the analysis at seven days.
		These show you the time to event analysis which was prespecified in the protocol and as published in the paper.  You will see the curves diverge for the first three or four days and then they remain absolutely parallel for the next few days indicating no evidence of an early rebound that has been of concern with antithrombin therapy.
		Again, for CV death, myocardial infarction, and refractory angina the same pattern of the difference emerging in the first three to four days and the curves remaining parallel on this slide up to seven days.
		These are the data on each of the individual components at seven days and at 72 hours.  At both time points you will see numerically there are lowering rates of cardiovascular death, myocardial infarction, and refractory angina so that for the primary the prestated key second re-endpoint each component contributes to the difference observed.
		Now, we further have provided in this slide key descriptors of what we mean by refractory angina.  Cardiac catheterization only was in 49 cases in the unfractionated heparin group and 55 in the lepirudin group and it was not different.
		However, there was a difference in the rates of PTCA, 29 versus 15.  CABG surgery 18 versus 15.  Need for urgent thrombolysis and transfer to a tursery center for intervention.  
		I will show you in a minute that the majority of these people indeed had intervention.  After being discharged, a few people were rehospitalized with unstable angina and this was part of the prespecified definitions and this was lower.  You will see there is a clear difference in those with ECG changes, i.e., objective data, and no difference in those without objective data.
		In the next slide I will show you details of those who were transferred from centers without cardiac catheterization facilities to those that had it, 53 versus 34.  Before this judge at that same rehospitalization all but one in each group had an intervention.  Before midnight after the day of pain onset, 31 versus 20 difference.  Later during the hospital stay 21 versus 13 and no intervention was done in one patient each.
		I don't have a slide on the data on rehospitalization but we've just looked at the results to see what happens to the rates of intervention in them.  If you give me a minute, I'll tell you what it is.  Out of the 14 people here and eight people here, in these 14 people 12 had an intervention, and in these eight, seven had an intervention.  The majority of the difference in refractory angina in the OASIS-2 study stems from the description of refractory pain, new ECG changes, and an intervention.
		These are the data on any interventions.  The previous was urgent interventions.  These are on any interventions at seven days.  You will see there's a 16 percent risk reduction which is nominally significant.  The entire difference in that comes from differences in the rates of PTCA.
		This is a summary of the results on the prespecified endpoints at seven days which was the primary point of evaluation.  There is a reduction or lower rate of cardiovascular death on new myocardial infarction with the confidence limits just crossing one.
		There is a clear reduction in cardiovascular death, new myocardial infarction, or refractory angina and there is a similar order of magnitude of reduction of cardiac interventions of any kind within the first seven days.  All of these point estimates are approximately the same.  
		The differences in these two are larger and emerge entirely during the treatment period which further adds plausibility to the differences observed here.
		This slide shows you the data from 72 hours up to six months.  The key point here is to show you that the differences that emerge in the first 72 hours persist right through up to 180 days.  The difference of about .6 to .7 percent in absolute terms emerged early, 2.6 down to 2.  During treatment is persisted out to seven days.  It was about the same at 35 days and about the same at 180 days. 
		This indicates that three days of treatment whatever benefit is observed persist long-term and there is no evidence of loss of that benefit.
		The next slide shows you the same data on the triple endpoint of cardiovascular death, myocardial infarction, and refractory angina is approximately a one percent difference a little less early, slightly greater at seven days, and it's about the same right throughout.  Again, this indicates a persistence of the early benefit.
		These are the data on non-cardiovascular deaths.  There were no deaths in the first seven days classified as non-cardiovascular in both infractionated heparin or lepirudin.  Between seven days and 35 days there were eight deaths in the unfractionated heparin group and three deaths in the lepirudin group that were classified as non-cardiovascular.
		At 180 days there was a total of 30 versus 20 and these again indicate that this classification of using cardiovascular death in our analysis as opposed to total death certainly does not exaggerate the difference between the various groups.
		The sponsor had prespecified in its analysis a modified intention to treat analysis which excluded people who did not receive any drugs.  You will see the difference between these two is only about 60 or .6 percent in this 10,000 patient population.
		I have presented to you the intention to treat analysis which is what we as investigators publish.  You will see the results are almost identical on the primary endpoint at seven days and at the second re-endpoint at seven days and the p-values are almost identical and hardly change.  	This indicates the robustness of the data and also indicates that the entire difference has emerged from the people who were treated.
		As you know, in this part of the trial as well patients were randomized if eligible to the warfarin component.  Only about 20 percent of the people received warfarin in this trial and it was balanced between  unfractionated heparin and lepirudin.
		These are the overall data showing the relative risk reduction of .84, whereas these other data on the non-warfarin patients, which is almost identical, with confidence limits overlapping.  These indicate that the randomization to the warfarin in no way affects, or at least in no material way affects the overall results of the trial.
		This is the summary of the results from OASIS-2.  In this trial lepirudin appears to be superior to unfractionated heparin.  On the prespecified endpoints at the prespecified time of seven days there is consistency across all three endpoints.  On the primary endpoint of cardiovascular death and myocardial infarction there's a 16 percent relative risk reduction with confidence intervals from -3 percent to 31 percent which is a p-value of .086.
		On the second re-endpoint there is also a reduction on cardiovascular death, myocardial infarction, refractory angina, which is an 18 percent risk reduction.  That is nominally statistically significant with confidence limits between three percent to 30 percent.
		The need for any intervention is also reduced by 16 percent which is nominally significant.  The differences in these two endpoints entirely emerge during treatment, so at the end of 72 hours there's a 24 percent risk reduction on cardiovascular death and MI and a 22 percent reduction on cardiovascular death, myocardial infarction, and refractory angina that is nominally significant.  	Extended follow-up at 35 days and 180 days indicates preservation of absolute benefits.  Now, about --
		DR. PACKER:  Salim, could you pause, please, and we'll open it up for questions on OASIS-2.  I'll begin with our primary viewer Dr. Borer.
		DR. BORER:  Salim, I want to ask a couple of methodological issues and then a little bit about the data.  First, I would like to echo what rob said.  That is, in the first question I asked I am not in any way suggesting that anybody did anything inappropriate, but I would like to know how tight the blinding was in OASIS-2?  
		The reason I ask the question is that within out briefing documents it appears that some patients were begun in OASIS-2 on a therapy that they should not have received and that therapy was then changed after they had begun.  How could they have known after the wrong therapy was begun that it was wrong?
		DR. YUSUF:  What happens is -- and this is something we do in every trial including HOPE and the same thing actually happened in HOPE as well.  People call in to a central number and they are given an allocation number, a package number, whatever it is.  You know, a seven-digit number.
		They could do one of two things.  They could write the number wrong and take the wrong package.  As soon as they randomize they access a page that has the information they gave us over the phone on patient identifiers and they write the treatment package as well.
		Whenever there is a discrepancy between what's reallocated in our central computer and the centers which means they misheard the allocation, we immediately get back to the center and say, "You've chosen the wrong package.  You must go back to the package that was allocated."  Neither we, that is the staff who did it, nor the center knows what it is.  It is simply based on the discrepancy between the package number they wrote and the allocation number we gave.
		DR. BORER:  Okay.  So nobody knew what was being given.  They just switched packages.  This, as I recall from the briefing document, and correct me if I'm wrong, the actual change occurred several days into the treatment.
		DR. YUSUF:  Sometimes the centers did not send us the fax.  They meant to send it to us within 24 hours.  Sometimes they took another day.  Remember treatment is only for three days so you can't do anything.  When we weren't able to change the package to the truly allocated package, the analysis is intention to treat.  By that I mean what we intended centrally, not what they did there.  In a sense, Jeff, it is sort of slightly, very slightly sort of diluting out any result.
		Now, again, we don't know whether heparin -- they may have got heparin and we gave them another number that was still heparin, or whether heparin was switched to hirudin or vice versa.  I have no idea because based on just the fact we wanted people to adhere to the letter of the law of the protocol.
		DR. BORER:  Okay.  The point is that although now we know that they were switched from one to the other, they didn't know what they were switching from or two.
		DR. YUSUF:  Neither did we know.  Neither did the staff know.
		DR. BORER:  I'd like to ask a little bit more about the potential for a warfarin-based confound.  Here again, it seems as if there were far fewer patients included in the warfarin follow-on study or substudy than were expected or anticipated suggesting that as you described for OASIS-1 there may well have been some bias on the part of investigators to enter or not to enter patients.
		That wouldn't necessarily -- that might concern me even though you showed a slide in which the results in patients with warfarin and without warfarin look fairly similar.  Still, there could be a confound but in our briefing document, there were data presented from centers that were pooled that didn't have warfarin available.  
		Those data really looked very different, to me at any rate, than the data that you showed us for with warfarin and without warfarin in that it looked as if the treatment effect was, at best, minimal in those sites where somebody couldn't be biased to giving warfarin or not giving warfarin because they didn't have warfarin to give.
		Now, I understand this is a post hoc small analysis of a relatively small subgroup, but I would like to have those data shown if you have a slide of them or, if not, at least I would like you to discuss how we got to that result.
		DR. YUSUF:  Is this the one you mean?  These are always --
		DR. BORER:  Yes.
		DR. YUSUF:  Okay.  So you will see these are 2,000 people who were randomized to active warfarin standard therapy.  This is the randomized part of the trial.  These are the people that got randomized.  These are the people with no warfarin available.  These are the not randomized.  No warfarin available was -- these are not by center, Jeff.  At the beginning of the trial the sponsors weren't able to secure warfarin and deliver it to the centers so we started.  This not randomized is then the rest where a physician said "I've done a PTC or a cath or somebody bled or I don't want to put them into the warfarin part."  Although we didn't make it optional, in the end that's what it turned out to be.  
		We have also done an analysis in two ways.  I don't know, Matthias, if we have slides.  We did an adjustment, you know, to see whether warfarin makes a difference and it doesn't.  The second thing is this group was equally split between hirudin and heparin so that would not -- as you can see, these are the event rates but the ends are the same.  
		All of these the ends are the same and there is no obvious imbalance in baseline characteristics.  In a way you could think of it like any other treatment like beta blockers being given.  Some centers use it and some don't.  When the ones that use it, they use it in some patients and they don't use it in others.
		DR. BORER:  You could think about it that way but as I look at the data, it appears that there is a difference or a suggest of a difference among those who were given warfarin in terms of treatment effective versus those who weren't versus those in whom no decision could be made because it wasn't available.  I just raise that as a concern.  Obviously we can't resolve that.
		DR. KOCH:  Your concern is addressed by the p-value of .964 which you see which is comparing the differences of .7 percent, .4 percent, .4 percent, and .8 percent with one another.  Although that is a low-power test, that is a test which is looking at whether the heterogeneity across those four groups has any realness to it.  It's basically random.
		DR. BORER:  I'm sure that you're right.
		DR. YUSUF:  There's one other thing I can help you with if you don't mind, Jeff.
		DR. BORER:  Let me make just one point if I may.  I feel uncomfortable saying this because I'm a cardiologist and not a statistician and you're a statistician so you know more than I do about this.  I think it's unfortunate to suggest when a p-value doesn't make it, and this obviously is way off, but p-value doesn't make the nominal statistically significant cut point to say, well, that happened because we didn't have enough power.  That's one possibility.
		Another possibility is that there is no effect and we have to consider both.  A nonsignificant p-value in a low-power test doesn't necessarily prove anything to me.  If I said that wrong, say it right, please, Tom, or Dr. Koch.
		DR. KOCH:  Yes.  I appreciate your concern but you should also appreciate that the patients who were not randomized at all had a magnitude of effect that was greater than or equal to the magnitude of effect that you're seeing in the warfarin subgroup.  For the most part, the differences in the magnitudes here are all relatively small so there's really not much you can do with this.
		DR. BORER:  Okay.  I don't want to belabor that.
		DR. YUSUF:  I want to give you some biological data, Jeff.  One thing, just to look at this group non-randomized, because obviously if you look at this group, you see that is almost identical to the overall result.  
		The next slide.  It's worth noting that treatment with warfarin was initiated at a median of just under three days.  Okay?  And as we all know, it takes three to four days to get a warfarin effect.  Now, this is showing you that the entire difference of warfarin occurred at 72 hours before you were able to get the warfarin effect.  
		Warfarin was just given about 2.8 days or so was when it was started.  You know it takes three doses at least to get an effect.  Biologically the entire difference is occurring before the warfarin is having an effect so this is just random chunks. 
		DR. BORER:  Well, perhaps but, again, we're not going to resolve that here.  Let me ask another question about your slide on -- in our slides it's page 48, OASIS-2, CVD/MI/RA absolute and relative benefit over time, intention to treat analysis, and the preceding slide where you show the deltas.  
		These deltas in absolute terms are very small and that's understood.  As a percentage change they are perhaps more impressive.  The absolute values are small and I don't know that one can say anything that is statistically meaningful about the variation.  		It appears to me that the deltas do get smaller over time.  Now, you are looking at a seven-day endpoint.  But in terms of the potential clinical utility of a therapy, if you know you're going to be losing benefit over time, then the strategy would have to be evaluated in the context of some additional management strategy to maintain benefit, I would think, or you might say that.  
		You dismissed the differences in these deltas as being basically insignificant or unimportant.  I shouldn't use insignificant but unimportant.  Yet, I see what looks like a trend to loss of benefit.  I wonder what you think about that?
		DR. YUSUF:  I think conceptually on the fact that any short-term treatment must be followed by long-term treatment.  I completely agree with you, Jeff.  That's really why we in our group pursue long-term therapies.  We try to do it with warfarin but it was a failure because people didn't like to use warfarin.  Conceptually I don't think three days of therapy with anything is the magic answer, you know, any drug.
		The second thing is with this therapy all we're saying is there's a difference that emerges early and there is no evidence that it is really -- no clear evidence that it actually is lost.  If you don't mind, when we get to the combined analysis of the two trials, you will see the numbers being slightly larger and more stable over time.

		We also have certain post hoc analysis which, if you'd like, I could show you which looks at higher risk groups.  You'll see it is maintained over time.  I agree with you that the difference is modest but remember it only emerges after three days of treatment.
		As a clinician I want treatments I can use long-term as well.  I think combination therapy is the way of the future.
		DR. BORER:  I just want to clarify one further methodological point.
		DR. FLEMING:  Jeff, before you leave that point, let me just --
		DR. BORER:  Oh, I'm sorry.
		DR. FLEMING:  I think the best -- I think you are raising an issue that for me was also a significant concern and I think the best place to look at this is in the briefing document on page 22 in section 421 where we have the exact data.
		The issue that we will be discussing, probably several times later on, is what is the relative importance of a result at seven days versus 35 days versus 180 days.  Thirty-five and 180 days were secondary measures in the trial.  
		We've had extensive discussions about this including in the last meeting that this committee had in October as we were discussing what would be appropriate criteria for trials in this setting.  Clearly there was considerable debate about the seven versus 35 days as being the proper primary endpoint.
		At a minimum a criterion is that the difference that you see in numerical magnitude must be maintained over time.  At seven days, for example, on death MI we have a difference of 211 events versus 178 events which is in excess of 33 events.  
		In a relative risk that .83.  That relative risk becomes .95.  As you go out to 180 days, i.e., a 17 percent reduction becomes a five percent reduction predominately because there are a large number of additional events that were anticipated to not be effective.
		But it is of interest that the delta, the excess number of CV deaths and MIs that are prevented that were 33 dropped to 24.  That's about 27 percent of those excess deaths and MIs are lost so you're observation was certainly consistent with mine.
		When you look at the triple endpoint and adding refractory angina, the relative risk at seven days, .82 goes to .96 so a 16 percent reduction to a four percent reduction or four-fold diminishment in the relative risk.  One might say that's because there are a lot of events that weren't expected to be affected longer term.  
		The excess number of prevented CVs, new MIs, and refractory anginas that were 57 dropped to 29.  Not only is it that we're seeing a lot of events that weren't expected to be effected but those that were prevented, 57 numerically, it's in half.  It's only 29, by day 180.  So I look at these data and concur with you.  I see that there is evidence to at least suggest that some of this excess that's prevented at day seven is not sustained longer term.
		DR. FISHER:  Can I make a comment here?  I've heard Tom talk about this before and we disagree in various ways but I think it's important people understand the implications here.  I actually agree with the sponsor that things look like they're maintained but I have told them they're lucky because you're adding so much additional noise it wouldn't be surprising actually if there were bigger drops and Tom can do the math as well as I can.
		If, in fact, the standard were to be that short-term interventions expected to have effect in an acute setting have to be maintained for six months, and in a setting where most events are going to occur elsewhere, you'll be talking about trials up in the hundreds of thousands.  I mean, in order to have adequate power.
		This is a tremendously large issue for drug development.  In fact, it would also suggest action to withdraw the approval of a number of additional things also.  We can look at it but I think Tom would certainly agree with me and Jeff as well that when you add a lot of additional events, you're going to have quite a bit of variability.  That's just the reality of the statistics.
		As I mentioned, I actually think it wouldn't have been surprising if the drop had been even more or you could put things together and it can go the other way but there's a huge play of chance as you get out and add a lot of additional noise and I think that is very important to consider.
		DR. YUSUF:  Actually, I can shed some data on that.
		DR. KONSTAM:  Can I just -- I mean, I just want to -- yes, Lloyd, in that case why look at six months at all and what would you have taken at six months to say, yes, there is a suggestion that the effect is going down as Tom has suggested.  Why look at six months at all based on what you're saying?
		DR. FISHER:  Well, as I mentioned, this is a very difficult issue because it wouldn't be at all surprising -- and it's important for other sponsors developing compounds in similar situations because they are tremendously at risk in the play of chance.  		Even given the fact they think they have the plan they are studying on, their biostatisticians can easily give them the distribution of the changes out par.  Certainly I agree.  I would be disturbed if it had entirely disappeared, although actually that would also be consistent with chance.
		DR. YUSUF:  Can I shed some light on this?  Can I have slide 57 of my main presentation?  These are data from both studies because exactly the opposite happened in OASIS-1.  The curves became more exaggerated with time, and this is the point Lloyd says, that the play of chance can be in your favor in one trial or against you in another trial.  
		You will see here, and I hope this is reassuring, this is what the two trials together, the totality of the evidence on CV death/MI is.  It's really no hint of a loss of that.  
		Jeff, we're doing a analysis of all the thrombin inhibitor trials.  At least up to 35 days we have been able to get the data from the big trials and there is absolutely no difference, no loss in the benefit that you see at 72 hours.  It's just parallel.  If this is a crucial issue, we can give it to the agency.
		DR. BORER:  Okay.  I have one additional question.  I just want to make the point here and it doesn't require a discussion and it doesn't require a defense.  
		I agree that a three-day treatment shouldn't necessarily be shown to have a persistent benefit six months later by itself but if it doesn't and the goal is to prolong life or prevent major events and you can only do it over three days or four days or five days, then it seems to me it's incumbent upon those who would propound the use of that treatment to show what the follow-on treatment is that does maintain the benefit.  Otherwise, you are exposing people to risk for no apparent benefit.  Again, that's in the record now and it doesn't require a discussion.
		DR. KOCH:  I think the only further comment that could be added to that is that because as the rates increase, the variability increases and you don't have statistical power at those later times.  All you can show are favorable trends.  You cannot demonstrate significance in the usual way.
		DR. BORER:  One final question here if I can find it.  I think you may have answered this already but I want to know the differences in the 63 patients that were excluded from the ITT for the MITT assessment.  If I understood correctly, you actually answered that question earlier in that most of these people never got drugs.  Can you say it again?
		DR. YUSUF:  Except for three.  I think three people were lost to follow up at that stage.  Is that what it is?  Okay, Gary, you have the numbers.
		DR. KOCH:  M-105.  This is the display showing the patients that are not in the MITT.  It's also showing the patients who were crossed over.  That is, 10 patients originally assigned to lepirudin.  Sorry, 10 patients who got lepirudin should have gotten heparin and five patients who got heparin should have gotten lepirudin.  None of the 30 patients at the bottom had events so the patients who had a misrandomization did not contribute either way.
		M-106.  These are the patients who were excluded from the MITT because they never received study drug.  There were two patients who didn't have a seven-day endpoint and neither of them had events.  Among the 63 excluded all together, there were two patients with CVD or MI added to the heparin group or added to the lepirudin group.  Basically these are pretty much what you would expect by chance.  The exclusion from the ITT is a chance type event.
		DR. BORER:  Thank you.  Milton, I'll hold my other questions.  They are not on primary data clarification.
		DR. PACKER:  Ileana.
 		DR. PIÑA:  Salim, you seem to have abandoned the severe angina as an endpoint here.  And then at the other endpoint you pooled out the revascularization issue.  Why did you do that?
		DR. YUSUF:  I think we were going for clinically more important endpoints in the big study.  Second, being an international trial, severe angina was going to be a nightmare to adjudicate.  We actually found that because we had to get every episode of recurrent angina and it would have just drowned us in work.  
		We wanted to go for the more clinically relevant endpoints.  The refractory angina we felt was pretty objective.  We could document it.  We could verify it.  CV death/MI obviously was that so that was one.  Interventions obviously has health care resource implications so we wanted to find out information on that.
		It was also mentioned in the protocol for OASIS-1 but we knew the event rates would be so low there wasn't going to be much in it.  I'll show you some data on it as well.
		DR. PIÑA:  Don't you think that is very geographically mediated?  In other words, there are some countries that will do this very often and some that just won't?
		DR. YUSUF:  You're absolute right.  There are geographic variations so the analysis was stratified by center because obviously a center with a cath lab will do it more often than a center without a cath lab.  The analyses on those -- in fact, all our analyses are stratified by center which takes into account region as well.
		DR. PACKER:  Paul.
		DR. ARMSTRONG:  Can I just follow up?  Salim, the definition of refractory ischemia was different in the OASIS-2 than the OASIS-1 study.  How did the new definition affect the frequency of refractory ischemia as previously defined in OASIS-1?
		DR. YUSUF:  It would have a minuscule effect and the reason for that is when we did OASIS-2 because of the fact that practice patterns in different countries were different in terms of discharging people earlier out of the hospital.  Based on our registry we had found Australia was the one that was discharging people the earliest, U.S. the next, and then the other countries kept them in the hospital.
		We needed a mechanism of capturing events all up to the same day.  That's why that was brought in so OASIS-2 actually has an added criteria compared to OASIS-1.  I showed you the rehospitalizations for unstable angina on one of the previous slides.  I don't know if you recall that.  That is the difference.  
		As you can see, they got rehospitalized within seven days so this is being discharged at three days to being rehospitalized before seven days.  That's the data.  There was a difference but the entire difference was in those who were rehospitalized admitted to a CCU, had EGC changes, and had an intervention.
		DR. ARMSTRONG:  So when you used the new definition the event frequency of refractory ischemia in OASIS-1 went down or up?  I'm just not clear.
		DR. YUSUF:  We don't have a way of using it in OASIS-1 because, for one thing, I think patients were by in large discharged around seven days in Canada.  Not all but by in large.  We are not able to retrospectively go back and do that analysis.
		DR. PACKER:  Jeff and then Joann.
		DR. BORER:  I'm sorry.  Just one more methodological question or analysis question, I guess.  I asked you and you answered what the nonstudy heparin issue was in OASIS-1, but nonstudy heparin also was given in OASIS-2 and there are larger numbers here.  		Do you have an analysis that would tell us what the potential or actual effects of nonstudy heparin -- I don't care about heparin that was given before so much as heparin that was given after the three days of therapy, what impact that may have had on outcomes with and without lepirudin.
		DR. LUZ:  Can I have 042?  This slide shows you the influence of nonstudy heparin on both the double and triple composite endpoints in seven days.  There are several observations that one can make.  First is that the use of nonstudy heparin within 24 hours after end of the infusion was higher in the heparin group than was in the lepirudin group.
		Second, and this is not unexpected, the event rates for both the double and the triple endpoint were higher in patients using nonstudy heparin after the end of the infusion because in many cases those patients had ongoing symptoms and this was actually the reason why they were put on heparin.
		Second, the difference between the two groups, if anything, was slightly bigger, at least in absolute terms, than in the overall population.  Importantly, the entire difference was accounted for by the treatment period, i.e., the period during which the active study medication was given.  
		If you look at this slide, you'll see that in the time between end of study infusion in seven days, the difference is actually very minor.  The same is seen with the triple endpoint where you have a full percent absolute difference in all patients using nonstudy heparin but only one percent difference after the end of the study infusion, i.e., while nonstudy heparin was used.
		DR. YUSUF:  I think, Jeff, this is an indication that the symptomatic benefits of lepirudin persisted for a few days versus unfractionated heparin so it's 900 more -- 100 more in the unfractionated heparin group compared to lepirudin in that 900 versus 800 is highly significant but we're not making much of that because we really didn't specify that as anything.  The event rates were different.
		DR. BORER:  Thank you.
		DR. PACKER:  Joann.
		DR. LINDENFELD:  I'll save my question until we get into safety.
		DR. PACKER:  Okay.  Tom.
		DR. FLEMING:  In the adjudication process there were 25 MIs, is that correct, that originally had been identified by the investigators and were not confirmed?
		DR. YUSUF:  You're ahead of me, Tom.  Let me see.  Do we have a slide on the adjudication?  This is 1 or 2?
		DR. FLEMING:  I think it was OASIS-2.
		DR. YUSUF:  OASIS-2.  Do we have a slide on the adjudication in OASIS-2?  Okay.  Here it is, Tom.  This is the confirmation rates.  It's not the absolute numbers.  It's the rates.  You'll see cardiovascular death was 100 percent, new MI was 95 percent, 98 percent refractory angina.  These are for rehospitalization with ECG changes or without ECG changes.
		Do we have another slide with the relative risk adjudicated and non-adjudicated?  We have one.  I know.  Tom, here are the data for CV death and MI at 72 hours and seven days, adjudicated and the investigator reported.  You will see the relative risks are the same.  The p-values are almost identical.
		DR. FLEMING:  Can you go back one slide?
		DR. YUSUF:  Sure.
		DR. FLEMING:  So five percent of the new MIs and two percent of the new MIs were not confirmed.  I think what I had seen in the briefing documents was that there were 25, eight on Refludan and 17 on heparin.  This seems to be consistent with that, about twice as many on heparin.
		DR. YUSUF:  That's right.  So if you use the investigative report that the differences would slightly widen out.
		DR. FLEMING:  If we use the investigators, we would add back eight events on Refludan and 17 on heparin.
		DR. YUSUF:  On heparin.  That's right.
		DR. FLEMING:  And if that's at seven days and if there is an excess of 33 in the adjudication analysis, then wouldn't that difference of 33 excess drop to 24?
		DR. YUSUF:  No, it will increase 33 plus 11.  You have to add back.  It will go the other direction, Tom.
		DR. FLEMING:  Go ahead and show the second slide.
		DR. YUSUF:  The next one.  You see, you have one percent more events in the unfractionated heparin group in the investigative report.  Not one percent but .1 percent.  2.6 would go up to 2.7 and two remains the same.  Remember there's a little bit of rounding here.  Then for seven days this 4.2 goes to 4.3, 3.5 goes to 3.6.
		DR. FLEMING:  And the relative risks?     		DR. YUSUF:  Are essentially identical.
		DR. FLEMING:  Slightly less but essentially identical with the investigator.
		DR. YUSUF:  Yes.
		DR. FLEMING:  All right.  Could we see the same thing for the triple endpoint, though?  That looks like it went  -- 
		DR. KOCH:  Tom, whenever you maintain the same difference if the rates increase, the relative risks will also always mathematically increase towards one.
		DR. YUSUF:  So these are the triple endpoints, Tom, and this is the adjudicated on top and the investigative report.  You will see again they are essentially the same.  Obviously relative risk is sharpened here because equal numbers of people are being thrown out in both groups.  Well, similar numbers.  Equal is an exaggerated term but similar.
		In both cases all the analyses are nominally statistically significant.  In fact, in OASIS-1 it happened the other way around.  Adjudication brought the relative risk up rather than down so I think it's a random process. 
 		DR. KONSTAM:  Just to clarify, if you want back two slides in terms of the triple endpoint, there were more -- if you look at the 98 percent versus the 91 percent and there presumably that's an endpoint with a greater degree of subjectivity, there were more such events thrown out in the hirudin group than in the heparin group.
		DR. YUSUF:  Slight differences.
		DR. KONSTAM:  Okay.
		DR. YUSUF:  These are the data, Marvin, and it was done blind.  One can obviously argue they are not significantly different but these are the data and these are not -- all I can show you is the data.
		DR. KONSTAM:  So the only even really noticeable difference is the triple endpoint.  The significance level goes from 01 to 02.
		DR. YUSUF:  To 02.  They are consistent.  I think that's the point.
		DR. FLEMING:  There was an algorithm in place that if the seven-day form was missing that you would count the events as deaths or MIs if it was known to have occurred according to the FDA summary on page 13 of our briefing document.  How often was the seven-day form missing?
		DR. YUSUF:  Seven in each group.
		DR. FLEMING:  Seven in each group.
		DR. YUSUF:  At the seventh day.  We could have had it on the sixth day.  You see what I mean?  To be honest, we didn't put that algorithm in the investigation.  It was something the company had put in its plan.
		DR. FLEMING:  In those cases were there any situations in which death or MI or had occurred?
		DR. YUSUF:  I don't know the answer to that.  Is Janice here?  Okay.  There wasn't any.
		DR. FLEMING:  My last comment really is kind of a two-fold part.  It does lead somewhat into the concepts of the pulling of the data.  One of the issues that is problematic is looking at the clinical relevance of the effects of an intervention where you expect the influence on the endpoints to be early, to be in the first three days.  
		Yet, if in fact those differences that occur in the first few days are not sustained for a clinically reasonable period of time in any setting, we would discount those as being important.  As we have already begun the discussion at this session, it does impact how we interpret the primary endpoint and whether it should be day seven, day 35.  
		What's the relevance of interpreting day 180 if, in fact, we were to choose day seven as the primary endpoint and information on day 35 or day 180 is just used to show that you sustained the benefit.  		As Dr. Fisher and others have pointed out, myself and many others have discussed in previous sessions the down side of the sponsor.  The risk the sponsor takes there is with considerable variability that exist.  In those events that occur after the time you have an effect, you may randomly miss the event.  You may randomly miss an effect that is sustained.  
		Of course, the flip side to that is it's an effect that is very small in the context of what is really clinically important to these patients.  If you're looking at death and MI, and death and MI is an event that's going to occur in 10 percent of these patients, and only a small fraction of those are occurring in the period when the intervention has an effect, then it is true that you're going to have to have a very large trial.  
		But, then again, you need a very large trial in order to be able to discern the difference between an effect that is real and sustained versus one that doesn't, in fact, have persistence.  It's led many of us to say for this reason you shouldn't, in fact, rely on seven days hoping to see it sustained because by chance you may be unlucky and you do, in fact, need to be looking at differences of larger magnitude or over a longer period of time.  
		That leads me to my comment looking at OASIS-1 versus OASIS-2.  It is true that OASIS-1 tends to show the opposite, i.e., instead of losing eight or nine deaths or MIs you'll pick them up.  In a sense if you do a meta-analysis, everything will look fine.  		Actually, I'm more concerned by OASIS-1 data than reassured by OASIS-1 data.  The specific reason for this is that there is, at least by appearance, a striking inconsistency between OASIS-1 and OASIS-2.  
		I'm leading up to a question, Salim.  The primary analysis that we have been drawing attention to in OASIS-1 was the four component endpoint at day seven which is the only one that in a sense by rigorous statistical methodology might be called significant.  This corresponded to a relative risk of .56 or a 44 percent reduction in the event rate comparing control against the .4 dose regimen.  
		This 44 percent reduction in OASIS-2 on the same endpoint was only a 10 percent reduction.  The relative risk was .9.  Let me finish.  This, in fact, was seen across the board on other measures.  If you look at death and MI, the relative risk in OASIS-1 is .53.  The relative risk in OASIS-2 is .83.  
		The fact that the differences that there are, in fact, in death MIs and increase in the excess that's prevented between day 7 and day 180 whereas there's a decrease in OASIS-2 makes OASIS-1 and OASIS-2 even more inconsistent when you look longer term.  		The relative risk in OASIS-2 at 180 days is .95 on death MIs, whereas it was .76 in OASIS-1.  The exact same thing happens when you look at the triple endpoint as well.  There is anywhere from a three to five-fold larger effect in OASIS-1 than in OASIS-2.  
		Looking at OASIS-1 it's not surprising that one might have projected that it could have been plausible to achieve superiority.  I think you were targeting a 23 percent reduction in the sample-size calculations.  In fact, that was reasonable.  Looking at the OASIS-1 magnitude of effect it was even larger than that, whereas the OASIS-2 magnitude of effect was much smaller.
		I'm not reassured in this loss of effect by the fact that it's not showing up in OASIS-1 precisely because that's just adding to the ways in which OASIS-1 effects are strikingly different than OASIS-2.  Is there an explanation for that?
		DR. YUSUF:  First, I don't think the smaller the trial, as we all agree, the point estimate of the relative risk reduction is weaker.  Therefore, you know, all of us over years have tended to think of the confidence intervals around so when you look at the confidence intervals of OASIS-1 and OASIS-2, there is no heterogeneity in the results at any time point.  There's no statistical heterogeneity at any time point.
		The second thing, Tom, we all know that small trials, the best you can get out of it, even if you can get that out of it, is directionality of effect.  That's why we do bigger trials.  You're right.  In the large trial we expected a smaller reduction.  We designed it around that.  
		As you know, I have written for years articles saying that the real effects are going to be moderate.  In my mind I did not expect a 40 or 50 percent risk reduction so whatever I saw in OASIS-2 had wide confidence limits.  It was consistent with an effect at about 20 percent.  
		All I'm interested from OASIS-1 is that it gave me a direction that was promising enough to go to the next step.  Obviously, if you get a big difference early and there's no loss of that big difference early, you'll see a bigger difference late.  In some ways I completely agree with you.  Take a small trial but don't believe large treatment effects.  Believe it best the directionality of the effect.  
		Now, the best estimate of treatment from a bunch of trials is not choosing the most effective difference or the smallest difference.  It's to take a weighted average of all those.  As you know, that has been my approach for 20 odd years and that's what people have been doing.  
		If you take the aspirin trials, you'll get trials where there's a 50 percent risk reduction.  You'll get other trials like the Amos trial with aspirin which had a zero percent risk reduction.  We all accept that the best estimate of the effect of aspirin is the totality of the data.  The data from larger trials will contribute more to that totality than from the small trials for they all contribute.
		DR. FLEMING:  I'm not persuaded by a statistical argument that this is purely random variability.  Is there any other factor that you're aware of in the two trials that would explain what is from the estimates striking differences?
		DR. YUSUF:  We've looked for biases, as I've told you, and we've really looked as hard as we can and we have no evidence of bias.  I really believe it's random noise.  In the discussion part of the OASIS-1 paper, we said random play of chance may have exaggerated the differences so that when a larger trial is designed, we should look for more moderate benefits.  
		That's why when we went to the company we said we really need a much bigger trial, not another trial of using the estimates of effect size.  And, Thomas, you know that to be completely consistent with the way I've done trials over the years.
		DR. PACKER:  Rob.
		DR. CALIFF:  In light of yesterday I want to ask two quick questions.  First, the geographical distribution you label as North America but not U.S.  Two questions related to that.  First, how many patients were enrolled in the U.S?  And, second, how many African American patients and what were the results of those patients?
		DR. YUSUF:  I think there were about 350 patients from the U.S. in OASIS-2.  As you know, OASIS-1 was entirely done in Canada.  How many African Americans did we have, 60 or 80?  Eight in OASIS-2.
		DR. CALIFF:  Eighteen?
		DR. YUSUF:  Eighty, eight zero.  In OASIS-1 obviously we may have had one or two Blacks but certainly not African Americans but African Canadians.
		DR. CALIFF:  Again, I just want to make a point.  This is a real problem and I think it almost seems like in the panels I'm on now the majority of studies have almost no representation of black patients from around the world, much less --
		DR. YUSUF:  You know, what surprised us, Rob, was you know we did the study in Brazil as well as in South Africa and we just weren't getting Black patients in because, you know, I have an interest in ethnic variation in disease and I try to use my trials to study that but we just weren't getting them and the reason is at least in South Africa blacks have not yet got the epidemic of cardiovascular disease and I think the U.S. is leading the way amongst individuals of Black origin in getting the cardiovascular disease.  Right now as an inside we're doing studies in Africa and we're told that in the capital of Botswana, Gabaron, there's only 12 MIs a year.  This just illustrates how hard it is to get African Americans into trials.
		DR. CALIFF:  Certainly if products are going to be sold in the United States, we have 15 percent of the population, just to reiterate, that's being left out of the trials and it needs to be taken seriously by the companies that plan to make profits in the United States.
		The second question is women.  Because of the pharmacokinetics of the drug, you might be concerned about different outcomes in women and men in this case.  Do you have a slide that shows the treatment effect in women?
		DR. YUSUF:  Matthias?  I'm sure we do.  Subgroup by gender.
		DR. KOCH:  While that's being gotten, I wanted to respond to Tom's concern about OASIS-1 and OASIS-2.  Tom, while OASIS-1 did show a somewhat larger effect on the quadruple endpoint, it turns out on OASIS-2 the effect on the double endpoint was actually bigger in OASIS-2 than it was in OASIS-1.  I'm sorry.  I take that back.  It was on death.  I'm sorry.
		DR. YUSUF:  No, no, no.
		DR. FLEMING:  In every measure it is strikingly different.
		DR. YUSUF:  Sure.
		DR. FLEMING:  Anywhere from a three-fold to a five-fold.  
		DR. YUSUF:  Tom, one --
		DR. FLEMING:  You didn't volunteer, Salim, and I don't know how much to make of these but I've been trying to think a lot about what is different between those two studies and what could account for them.  Some of the things that come to mind are there is a differing heparin regimen in terms of how it's scheduled.  
		It may be small.  There is a difference, though, in the number of people that have increases in heparin dosing.  It's 33 percent in OASIS-1 versus 52 percent in OASIS-2.  The concomitant meds, as I understand, aren't exactly the same in the two trials.  OASIS-1 is not blinded.  We've talked a lot about that and whether that could impact and it possibly could.  		That was one of the ways in which it could be showing up.  There are some differences and there may be other ones that you are aware of.  The data are strongly suggesting that something is different in these two trials and to pull them, which is what we are about to do, is especially of concern when you are pulling results that are so disparate.
		DR. YUSUF:  Tom, the differences between OASIS-1 and 2 in results are identical to what you would see between trials in any area that when you try to pull -- when we did the thrombolytic trials.  The smaller the trials, the greater the heterogeneity results.  I really think -- I truly believe, and honestly this is not because I'm standing here, I truly believe it's the play of chance.  
		I've wrestled about this for years.  You get small trials and the point estimate is the least unreliable information from it.  The best you can do from that is look for directionality of effects and use the data toward bringing together all the information to get the best point estimate.
		DR. FLEMING:  Well, the key is and philosophically what you're saying, I think, and we don't need to get into an extensive statistical discussion about this, but the essence is, and I agree with you, the OASIS-1 trial is a very small screening trial that was done to provide important insights to the design of the OASIS-2 trial.  
		One of the unfortunately things about it is it gave us a strikingly higher estimate of efficacy leading us to expect the 23 percent reduction, at least, in the sample size calculations of OASIS-2.
OASIS-2 has 20 times the data.  The essence of the interpretation of efficacy is really driven by the OASIS-2 trial.
		DR. FISHER:  I wanted to make another point.  Tom brings up an issue which is important, but you should remember that under the no hypothesis of no difference if the true odds ratio is one, you can combine all sorts of disparate trials.  Where you run into trouble is when you think there is an effect and you look at these different odds ratios and try to understand why there's a difference.  	And then for the estimate of the effect that people might expect in different clinical settings it's very important.  		Under the no hypothesis of no effect in either trial, then as all we statisticians know, I think, it would be appropriate to pull them because you are just trying basically at that stage to say, yes, there's good biological activity.  
		Tom's concerns are actually more directed towards -- well, forgive me, Tom, because he won't say this, but he is mentally thinking, "Well, gee, if there's an effect here, why does it differ between these populations and this sort of magnitude."  
One argument which is perfectly consistent with the data is chance but that doesn't prove it, as was mentioned.
		DR. FLEMING:  Lloyd, since you're at the mic, you made an important insight at our meetings in August that were coordinated by FDA and the Duke group leading up to the October meeting that we had here of the advisory committee looking at criteria and design guidelines.  One of the issues --
		DR. FISHER:  I now deny whatever I said.
		DR. FLEMING:  It was intriguing because you had pointed out that if you do a meta-analysis and you do so, for example, with a random effects model acknowledging the variability that can be existing among studies, you pointed out the paradox that if you have one trial that shows an effect and then you have another trial that shows a strikingly bigger effect but highly disparate in the magnitude from what the first trial showed, that a meta-analysis with a random effects model will actually give you an attenuation or a lower sense of --
		DR. FISHER:  Well, no.  You can even lose everything.  I've made the point even more extreme than that.  If you have to be able to assess for possible differences between trial, that means one large trial, no matter how convincing, that's just one trial.  Throw it out because there's no way of estimating inter-trial variability in the same context.
		Most of these trials, of course -- and it could be there's differences because Canada is in one part and the rest of the world is in the other.  There's a lot of hypotheses we can come up with.
		DR. FLEMING:  This, Lloyd, is one of those situations so essentially we could spend all day but time is limited.  My sense is from all of this there is enough that is perplexing about the inconsistency with OASIS-1 and OASIS-2 that -- and since OASIS-1 is only five percent of what the size of OASIS-2 is, OASIS-2 is the essence of the signal that we have.
		DR. KOCH:  Could we show E-187 just for purposes of completeness on this point?  This is the test of heterogeneity across the two studies for both the double and the triple endpoint either using all the doses of lepirudin in OASIS-1 or only focusing on the use of the middle dose in OASIS-1.  All four of these p-values are well above .10 so this supports that there is some homogeneity even though there certainly are recognized differences.
		DR. FLEMING:  Gary, that doesn't support homogeneity.  That is so underpowered.  It's saying relative to that particular measure, that particular assessment there is statistically convincing evidence of heterogeneity.
		DR. KOCH:  I understand the point you're making but the underpowered --
		DR. FLEMING:  Clinically look at the data.  There is a three to five-fold difference in the relative risk reduction.  That's striking.
		DR. KOCH:  I understand, Tom, but when you say the thing is underpowered, you need to recognize that OASIS-2 is a very big study so you are looking at OASIS-1 relative to the standard that is expressed by a very large study.
		DR. FLEMING:  And we all come back to the same point and that is the main signal here is OASIS-2.  You have 20-fold as much data and the only reason statistical tests of certain choices don't pick up as being statistically significant is the small sample size in OASIS-1.
		DR. LUZ:  I agree but one additional comment.  OASIS-1 is a purely Canadian study.  OASIS-2 was a world-wide study but it had a considerable Canadian proportion.  If you compare OASIS-1 with the Canadian population included in OASIS-2, you'll find first that the baseline characteristics match almost perfectly.  Second, that the magnitude of effect is, in fact, very comparable between OASIS-1 and this subset in OASIS-2 with the point estimate for heparin being exactly the same in both studies.
		DR. YUSUF:  There is a slight modification, like Matthias said, which is the relative risk in OASIS-2 in Canada was slightly better than the rest of the study but it didn't get exactly to that level.  Isn't that right?  It didn't get to what we had --
		DR. FLEMING:  I was going to say the OASIS-1 and the OASIS-2 data together next.  I was hoping to see the outcomes in women.
		DR. DIMARCO:  Mr. Chairman, why do we have to see the -- I mean, we've already seen OASIS-1 and we've already seen OASIS-2.  I think the committee members can add.  Why do we have to see them put together?
		DR. YUSUF:  I would like to show them to make certain points, John, if you don't mind, please give me five minutes and we're done.
		DR. PACKER:  Before we go on I just want to see if I clarify this because the statistical issues that have been raised are clearly important.  I must say being a nonstatistician we as a committee all of us who are clinicians struggle with how to weigh the statistical issues.
		I guess I must say that I'm looking at this increasingly and feeling like an old country doc when it comes to fundamental principles of drug development.  Let me see if I've got this right.  
		Salim, you did a study called OASIS-1 which was a pilot trial, a trial which for all the reasons that have been mentioned it was considered to be a pilot trial.  It was a small study.  It didn't really have a primary endpoint.  It didn't really have a statistical plan.  
		It really was an exploratory trial.  It allowed you to set up a hypothesis that was attested in a big study, a definitive trial, a blinded trial, a trial with prespecified primary endpoint and assigned alpha, a trial that allows you to specifically address whether a preliminary finding is OASIS-1 was real or not real.  Is that correct?
		DR. YUSUF:  Partly.
		DR. PACKER:  There cannot be any other way of thinking about this.  The documentation that OASIS-1 was a pilot trial for OASIS-2 is undeniable.  You created OASIS-2.  You set up the rules.  You said the primary endpoint is cardiovascular death and new MI at seven days.  
		You said that you were going to test that at an alpha of .05 which after corrected for interim wilks is .048.  You then pick the secondary endpoint, assign an alpha of .01.  I'm not exactly certain how you got all that .01 to spend having spent it on the primary but, nonetheless, you've got a secondary endpoint with an alpha of .01.  	You needed to achieve a .048 for your primary.  You got .0863.  You needed to achieve .01 for your secondary.  You got .0163.  		What are we talking about here?  You said you were going to do something.  You used the data from OASIS-1 to set up OASIS-2.  You did not achieve what you said you were going to be accountable to in OASIS-2.  How can you declare victory having lost?
		DR. YUSUF:  Okay, Milton.  This is getting interesting.  I think it is how you view evidence and whether you view evidence on a sole isolated p-value or on coherence of information from the totality of the data.  We have been very frank, fair, open in presenting the data.  The good thing is we all agree what the data and the p-values are so that's good.
		Now we come to the more interesting part.  I have believed, and so to a lot of people, that if you hit a certain p-value and you are just above or below it, it's not as if the evidence changes qualitatively.  If you are far away from the p-value, sure, but if you're close to it, you are left with a difficult choice.  In that circumstances, you look at first internal coherence, you look at the effect on other end points, you look at the effects on those end points in other trials, and then you say does the treatment work or not.  I think in the end we are trying to assess whether the treatment works, not whether a given p-value is the thing because the p-values are out there.  We all agree what the p-values are.  My point is please evaluate this in the context of the totality of the data.
		DR. PACKER:  But, Salim, if the p-value doesn't really matter, why are you showing us a meta-analysis?
		DR. CALIFF:  Milton, let me take up for Salim a little bit here on this one.  This is the crux of the issue that really is going to swing the decision.  After all, I think what this committee is supposed to do is to help give guidance or recommendations to the FDA about getting medical products available to patients if they are beneficial or withholding them if they are not beneficial or there is enough doubt and we are concerned that there is going to be harm from unleashing this on the public.
		There's no question under the way things have been done for the most part in the past the way you described it is exactly the way it's been done.  You do Phase II, you generate hypotheses, you test the hypothesis in Phase III.  That is nice, from my amateur statistician point of view frequentist view of the world.
		I completely agree with Salim that is not a very good way to look at the world but we are sort of -- and the issue that you're raising is whether I agree or disagree.  Can you change the rules post hoc from what you had said you were going to do.  
		I would argue that the best look at what a treatment will do when it's put out there is a combination of all the data that you have looked at in a reasonable way.  I think an effort is being made here to put that point of view forward.  It would be a change from the way things have typically been looked at.
		DR. PACKER:  It's more complicated than that.  We have a history and some confidence in the process of determining a decision based on certain a priori rules that we set up for ourselves.  We can do that for a single trial.  We can do that for a number of trials.  It is very hard to know how to do that for a meta-analysis.  It's hard to know.
		DR. CALIFF:  Well, you have more confidence than I do in what we've done in the last five years.  I think from this committee there have been several things we have put out there that turned out not to be so good because under the stringent rules we've set up, it might be better to design an experiment that was less relevant to what the product does when it's out there in the world because you can easily reach this level of proof of principle.  I'm arguing there may be another way to look at it that might be reasonable.
		DR. KONSTAM:  Milton, can I just chime in as well?  Salim obviously needs some help.  I think the statement that you made, I think we really need to defer, you know, on judgment here.  I think if you really want to get into it, they are not asking for an indication after all that the drug is better than heparin.  I think that --
		DR. PACKER:  Marv, no, no.  Please, we need to be careful because there is a sequence of presentations today which are very important.  The sponsor is concluding in their briefing document and in their presentation that the combined data from OASIS-1 and OASIS-2 provides persuasive evidence for the superiority of lepirudin versus heparin.
		DR. KONSTAM:  Well, I didn't see that wording in the indication so --
		DR. FISHER:  I was going to say maybe we ought to wait because this is an active-control trial and we seem to be forgetting that here.  I guess I won't go into the carbatalol story.
		DR. KONSTAM:  I didn't see anything to that effect --
		DR. FISHER:  But people have argued --
		DR. PACKER:  Why don't we do this.  Pause for a moment.  Salim, why don't you go on with your next few slides.
		DR. FISHER:  Just one other fact that Salim will soon say.  This combination was actually suggested by the agency.  It didn't come from --
		DR. PACKER:  Wait a minute.  Lloyd, what does that mean?  Is that a good thing?
		DR. FISHER:  Well, I'm sure within this room we can have a wonderful debate as to whether that's a good thing or a bad thing.  Most sponsors will try to bend over backwards to go along with what the agency prefers.  For example --
		DR. PACKER:  Wait a minute.  With varying degrees of enthusiasm.
		DR. FISHER:  That may very well be but, for example, I believe, and probably Tom Fleming believes for that matter, the modified intent to treat if you have good blinding is preferable because you eliminate noise and you have all the benefits of a randomized study.  We discussed all that but we said it's such a minor issue here and it makes no difference.  Throw up the ITT so that this will not be a big distraction.  
		As you'll see in my presentation, I think you can make a fairly strong case on the basis of OASIS-2 alone for approval.     
		DR. PACKER:  Okay.  Let's pause.
		DR. YUSUF:  At least let me present the data and then you can make the judgment. 
		DR. PACKER:  Dr. Talarico.  Hold on one second.
		DR. TALARICO:  There was no recommendation to make a definite combined analysis.  We could not find any statement that clearly stated that the two trials could be combined for the analysis.
		DR. PACKER:  Please let me reassure the sponsor that whether it was their idea or not really doesn't matter.  It doesn't matter.  Let's hear the analysis and let's see what we think of it.
		DR. CALIFF:  Milton, can I see the results in women?
		DR. PACKER:  Upon the combined analysis 
or --
		DR. CALIFF:  I'll accept either one.
		DR. PACKER:  Why don't we see the combined analysis first and then we can --
		DR. CALIFF:  Okay.  That's fine.
		DR. YUSUF:  Okay.  Can I have the next slide?  Now, as Milton said, I actually agree with Milton.  Even if the FDA did not say it, I would have done it because I always believe you look at the totality of the data.  Indeed, this is what we also did in the manuscript.  Apparently there is a paper trail that when meeting with key members of the cardio renal group, not with Dr. Talarico's group.  Dr. Talarico is right, there are some minutes somewhere -- I haven't seen it but I'm told there are -- that before completion of patient recruitment and before unblinding, that the two would be looked at together.
		DR. FLEMING:  Although, Salim, you would say the fact that it was before unblinding, that is, of course, not before unblinding of OASIS-1.
		DR. YUSUF:  Sure.
		DR. FLEMING:  So you already knew that you had really positive results.
		DR. YUSUF:  Yes.
		DR. FLEMING:  And it wasn't a particularly noble effort not to include it.
		DR. YUSUF:  Absolutely.  Tom, I'm glad you at least say some things come easy to me.  The next slide, please.
		So these are the results of OASIS-1 and 2 side by side and over all.  You will see side by side on the double endpoint of cardiovascular death and MI at seven days directionally there are similar results in the two trials.  The event rates are about the same in the unfractionated heparin.  As Tom pointed out, the effect size seemed to be somewhat larger.
		However, I truly believe the best estimate of the treatment effect is the totality of the evidence and these are the data on the combined analysis indicating a 19 percent relative risk reduction with a p-value of 0.033 which is nominally significant.  Not an overwhelming p-value but it's nominally significant.
		These are data on the triple endpoint cardiovascular death, myocardial infarction, and refractory angina.  Again, you will see these are the two arms of OASIS-1.  If you only included the medium arm, the results are somewhat better but these are the two arms because we are going to the concept of the totality of the evidence and you will see directionally similar results in the two trials.  As Tom pointed out, the data will be heavily swayed by OASIS-2 because it is 90 percent of the data.  You will see 6.7 percent down to 5.4 percent, a relative risk reduction of .8 with a p-value that is again nominally significant.
		The next slide shows you the data on therapeutic cardiac interventions up to seven days, directionally similar effects in OASIS-1 and OASIS-2. And the combined data indicate a 17 percent risk reduction that is again nominally significant.
On the three endpoints across the two trials, at least directionally the results are consistent.
		These are the data on looking at the durability of the effects on cardiovascular death and myocardial infarction using the totality of the evidence.  Again, you will see it's 2.7 percent down to 2 percent at the end of treatment which is a .7 percent difference which remains essentially unchanged right throughout the trial so that the only difference on the totality of the data is persistent right throughout.
		The next slide shows you data on non-cardiovascular deaths.  There were no 
non-cardiovascular deaths in the lepirudin group at seven days, but after that and by the end of the study, 34 such deaths in the unfractionated heparin group and 22 in the lepirudin group.  
		If you add this to all the others, we would show a slight divergence but I believe that would be inappropriate because I have no reason to believe hirudin or unfractionated heparin will have a beneficial effect on these endpoints.  Therefore, I believe the combined CV death MI is the right one to use, although this would exaggerate the p-value a teensy weensy bit.
		Therefore, the overall data from OASIS-1 and 2, the entire program, I believe, provides persuasive evidence that lepirudin is superior to unfractionated heparin in this population.  Remember, yesterday I used the word convincing.  Today I'm using the word persuasive.
		Now, this is based on the following, that cardiovascular death and MI and the triple endpoint are significantly reduced at 72 hours and at seven days.  There is also an additional reduction in therapeutic cardiac interventions at seven days.  
		There is at least directional consistency of results from OASIS-1 and 2 and no evidence of statistical heterogeneity on the results, although a strong point about that doesn't say we have homogenesis results.  The absolute benefits that we observed early are preserved long term.
		I think I should now say thank you very much.
		DR. PACKER:  Okay.  Marv, I just wanted to clarify the fact that both the sponsored document and the sponsors presentation, in fact, says either clearly superior or persuasive evidence for superiority.  Let me just make a point.  
		The reason for asking the issue is because if one concluded that this agent was superior to heparin, there would be no need for Dr. Fisher's presentation.  		
		If this committee believes in the conclusion stated in the last slide, then there would be -- we could shorten this meeting considerably.  That was the only purpose for my asking the question.
		DR. KONSTAM:  But nobody believes that.  		DR. PACKER:  We will find out.  We will go to now questions on the meta-analysis.  We'll begin with Jeff.
		DR. BORER:  Actually, I have no questions about the analysis itself.  I think the issue is the appropriateness of the combination and I think that is really for a later point in the discussion here.  I think you've presented the data and I have no more questions about the data.
		DR. PACKER:  I am a little bit remiss.  Dr. Califf really would like to see the data in women.
		DR. BORER:  That's a question.
		DR. PACKER:  Do we have the data in women anywhere?
		DR. YUSUF:  These are the data, Rob.  This is younger and older, males and females directionally similar results.  These are the data by race.  These are the data by weight and weight is an important issue as will be discussed later on the safety part.
		DR. CALIFF:  This is somewhat to make a point that I think particularly with drugs that are renally clear, we need to look specifically at women.  We are learning that about QT interval prolonging drugs and I think with any thrombotics that are renally clear because of that intersection of weight, creatinine, and gender.
		DR. YUSUF:  And we'll come to that in the safety because that's your concern.  Isn't it?
		DR. CALIFF:  Yes.
		DR. PACKER:  Okay.  Ileana, I think you were next.
		DR. PIÑA:  Salim, in your combination here of both trials, you have therapeutic cardiac interventions up to seven days.  Why did you include them when that alone was never an endpoint in OASIS-1 except as included in the definition of refractory angina?
		DR. YUSUF:  Why did we include that in OASIS-2?
		DR. PIÑA:  No, no.  I'm saying why do you use this analysis in the combination as if it had been an analysis separate in OASIS-1 when, in fact, it wasn't?
		DR. YUSUF:  When you do meta-analysis you try to get the same endpoints across all the trials as long as it was collected even if it's not "a prespecified primary or secondary outcome."  For instance, many years ago there were at least two instances -- there are three instances I know that this committee did use meta-analysis to assist in the decision making.  I was involved in three of them, or two of the three.
		The first was the aspirin meta-analysis going back to 1984, in which case no single trial had provided convincing evidence that aspirin post MI reduced CV death or MI.  Some trials had mortality as the endpoint.  Other trials had CV death as the endpoint.  Other trials had MI as the endpoint.  
		The people who presented it got the same endpoints from all the trials and put it together.  	When you do a meta-analysis what you're trying to do is totality of information and not any data derived emphasis.  
		The second thing was when we did the streptokinase meta-analysis, which I think Jeff was the chairman when that came to the committee, there were two bits of data that helped.  One was the GC-1 study which was clear on mortality.  
		The second part was the meta-analysis of 20 trials and there we had some trials that were small that were completely negative suggesting hazard like a two-fold hazard.  Others suggesting a 20 to 30 percent benefit but the confidence limits overlap.  There, too, some of the small trials, Ileana, did not have mortality as their primary endpoint.  
		They had changes in the thrombolytic system or patency but we got the mortality data.  The approach of using the same endpoint, even if that endpoint was not a primary or secondary endpoint, is standard in meta-analysis.
		DR. PIÑA:  In OASIS-1 did you collect cardiac intervention separate from refractory angina?  		DR. YUSUF:  Yes, we did.
		DR. PIÑA:  In other words, an investigator may have decided to do an intervention even in the absence based perhaps on cardiac cath data.  You had collected those.
		DR. YUSUF:  Yes, systematically it was collected on a standardized form.
		DR. PACKER:  Rob.
		DR. CALIFF:  I don't think anyone is going to argue with the numbers that you've aggregated here.  The numbers add up and I guess I've already said that in general I would be in favor more of development programs that stated out front we're going to combine all of our data because it seems to me that there is some risk and I'm sure it's happened to this committee before that you see the Phase III trial which comes in just under the wire but you don't see all the other data which may not be as favorable.  I guess the worrisome thing, Salim, I know you do have a long history of doing this but would you be up here talking about it if OASIS-1 had tended to make the data go the wrong direction?
		DR. YUSUF:  That's a good question and, in fact, we wouldn't be here.  In fact, I would have tried very hard to persuade the sponsors that the p that was just short of significant really was even more short of significance than what OASIS-2 showed because there is no supported data.  
		To me the concept of supported data and looking at the totality of the evidence is true no matter what intervention, no matter what the result of one of the trials is.  You are absolutely right.  Often when we are on the committee we are only presented with the best data.  We aren't presented with the all the data.  
		Let's think of a scenario where we have two trials done by a sponsor.  One hits 0.06 and another one also hits 0.06.  Let's say that the difference in area where one hits 0.04 and another one was p .10 totally, I would take the first one as being more persuasive than the second one.
		DR. CALIFF:  I agree with you but it's just that this wasn't laid out like this in the development program which is the point Milton made and that's the problem.
		DR. YUSUF:  And Milton is right, and actually Tom made a good point.  Remember when we did the OASIS-2 study we knew the results of OASIS-1 so had we even written it down somewhere we would combine the data, you know, in a sense it is based on our knowledge of OASIS-1.
		DR. PACKER:  Marv.
		DR. KONSTAM:  You know, I mean, isn't this something analogous to a regression to the mean in the sense that nobody would have done the second trial had the first trial not clearly pointed you in that direction.  I mean, to me any attempt retrospectively to combine them is sort of stacking the deck.  
		I think this is analogous to what Rob is saying.  You wouldn't have been doing it.  I think if OASIS-2 were more positive than OASIS-1, you clearly would not have bothered us with it.  I think it's something like regression to the mean.
		DR. YUSUF:  I think, Marvin, what you said is true.  We are doing a world-wide meta-analysis in all the thrombin inhibitor trials.  If you take all the hirudin data including some that were stopped because of "not favorable results."  
		The point estimates are identical to what we saw and the p-values are about 401.  Because of the format that here we only look at the evidence from one agent, obviously we can only give you the two trials with that one agent.  
		If you take the GUSTO series of trials, the TIMI-9 series of trials and you put it all together, you get the same result and it's there in our manuscript, in the Lancet manuscript.  That would probably allay some of your concerns.
		DR. KONSTAM:  I'm arguing that it doesn't -- you know, that I don't find it particularly valid to combine the two because --
		DR. CALIFF:  So, Marvin, you would just ignore all previous data?
		DR. KONSTAM:  No, I'm talking about this specific situation where you have two studies.  One was clearly performed as a pilot to the second and the second would never have taken place if the first had not been positive.  To then go back and say, okay, now to make the p-value work let's combine the two just doesn't seem valid to me.
		DR. YUSUF:  Marvin, we didn't make the p-value work.  In fact, if the p-value were wholly nonsignificant, we wouldn't be here.  That's right.  I think that most of you recognize that my approach to the evaluation of the data has always been on the totality of the data.  What I've done here is the totality of the data I have available to me.
		DR. KONSTAM:  I was just involved with a trial called ELITE-2 which was based on ELITE-1 which seemed like this amazingly positive p-value, and then ELITE-2 which was neutral.  I don't think that anybody could view justification to combine the two and say the right answer is the combination of the two.
		DR. YUSUF:  Can I just make a point which we may agree on.  We don't need to combine it.  Just look at them qualitatively side by side.  We would agree there is directionality that is similar on the same endpoints at the same time point.  The combination is only one step further but visually you would say in both trials the direction is the same.  Would we agree on that?
		DR. PACKER:  There are going to be philosophical issues that are of great interest and importance that will not be resolved today.  I think that we have to try to focus on the issues and the data at hand.  Let me ask the committee are there any other questions about the combined analysis?  Tom.
		DR. FLEMING:  I have two brief questions.  Let me just concur with the statement that we surely do want to look at all the data and that is always critical when an advisory committee is reviewing to know that, in fact, there are other studies beyond these two that are highly relevant to this issue.  
		We have to be confident we are seeing everything that's most relevant and we need to look at it in the totality.  It's the subtleties in interpretation that are critical and Marv is raising an important one about the regression of the main phenomenon.  Where we will have troubles here is when we put p-values on these meta-analyses differences and use that in some way as the basis for a conclusion, as Milt has pointed out, a conclusion of superiority.  
		I have just two quick questions.  At least one of them is really quick.  Given the imbalanced randomization, the 433 and the OASIS-1, I take it all of you estimates were based on stratifying by study taking into account the imbalanced randomization?
		The second point, and it's what diminishes my confidence that this meta-analysis is telling me something I can really interpret, is the heterogeneity, as I have mentioned, between studies.  		Dr. Fisher's insight last August on the difference between a fixed effects and random effects model when you're considering center as random effects, is really getting at what is intuitively of concern to me.  When you see such heterogeneity and the random effects model is particularly sensitive to that heterogeneity across studies.  I assume this was a fixed effect.
		DR. YUSUF:  This is a fixed effect.  We've also done it by random effects and obviously the p-values go up a little more, but in every case it's less than 0.05.  You're right.  I don't hang on the p-value.  I mean, I believe in coherence of information and so, you know, just to be reassured, if you do an random effects model, the conclusions still hold.
		DR. CALIFF:  I have a point.  Hanging has two meanings.  You said you didn't want to hang on the p-value.  It has two meanings.
		DR. YUSUF:  What's that?
		DR. PACKER:  It's okay.  He'll explain it to you later, Salim.  Any other questions or comments?  Okay.  
		What I want to do is take an unusual step because it's very relevant to the process that we are going through today.  There is no question to the committee specifically on superiority but it is very important in the thinking process of this committee and in the relevance of the presentation going forward to make a judgment here.  
		After discussions with the division, it seemed very appropriate to ask the committee for a vote on the issue of OASIS-1 plus OASIS-2 based on the issue of superiority.  The question to the committee is a very relevant question and we will discuss it briefly and then take a vote, a binding vote, on it.  		The question is based on the data from OASIS-1 and OASIS-2 individually or combined, depending on your opinion, based on the discussion that has been presented already, do you believe that there is reasonable evidence to support a statement that lepirudin is superior to heparin for the indication being sought?  
		Let me again ask the question.  Do you believe that there is reasonable evidence for a superiority claim for lepirudin over heparin for the indication being sought?  If the answer to the committee is yes, we can shorten this meeting considerably.  If the answer is no, we will take a break.  Okay?  Because if the answer is that it is superior, then the concept of putative placebo is irrelevant.  Okay.  Any discussion on this matter?  Jeff.
		DR. BORER:  Well, obviously what you're raising here is probably the most fundamental issue that we ever deal with at these meetings which is what are the standards of evidence necessary for approval of the drug.  The subhead here is what's the standard for equivalence or superiority versus an active comparator.  
		The secondary issue there would be the standard of evidence for superiority to a putative placebo all of which are separate but combined issues.  What we are being asked is whether the data in aggregate provides sufficient evidence to allow us to say confidently that lepirudin is effective, that it's not less effective and, in fact, it's more effective than a therapy commonly used in the community and that it's acceptably safe for its intended use.  
		What you're asking us really is to provide an opinion, if we're going to provide an opinion about this, to determine whether there is any objective standard that we need to apply or whether it's necessary to employ our collective intuition without any a priori objective criteria or do we somehow get in the middle of those two which I'm not sure how you would do.
		We also need to know whether it's necessary only to consider short-term benefit, to consider longer-term benefit, to require more safety information before we make this determination, and whether a follow-on strategy needs to be added on.  And we need to see an analysis of what happens after everybody gets the follow-in.
		There are all these questions.  I would have to say that at this point I think there are highly suggestive data that lepirudin may be superior to heparin but in the absence of more safety data, some further consideration of the short-term versus a longer-term benefit issue, I'm concerned about drawing a firm conclusion about this when the objective standards that we have commonly employed don't seem to be met here.  I would have to say, although at the end of the day I might vote for approval or something, at this point I would have to say no in answer to your question.
		DR. PACKER:  Discussion?
		DR. DIMARCO:  How can we talk about whether it's superior if we haven't discussed safety yet?
		DR. PACKER:  Because superiority is in the simplest term here efficacy.  Safety is going to --
		DR. DIMARCO:  But we're not comparing two dose ranging trials where we know we're at the maximum dose and since it looks like safety is proportional to efficacy to some degree, or inversely proportional to efficacy, I don't see why you want to talk about just efficacy until we've looked at the relative safety.  If there's a lot more bleeding with a drug and it's a little more effective in producing acute coronary syndromes, it may be superior but no one would use it and so why do we want to talk about it?
		DR. PACKER:  I guess the question is not so much a ruling on a claim the sponsor is not making or is not asking for.  The ruling is an assessment at this point in time whether the combined data from OASIS-1 or OASIS-2 together or alone allows for a conclusion that one is better than the other on efficacy parameters alone.
		The reason is that is not asked of us in any of the questions.  Otherwise, I would save it to the end.  Normally we would be asked to make that assessment separately for efficacy and safety anyway.  It is only in an attempt to move the discussion along in a logical fashion that I'm bringing that point, which is not mentioned later, up in the discussion at this point in time.  Any other discussion?  Rob.
		DR. CALIFF:  Well, I guess -- well, this is a tough one for me on this issue because there's no question about the standard of this committee statistically and this doesn't meet it.  Even the overview doesn't meet the standard of this committee purely statistically of the past which is .05 squared as we've talked about for primary endpoint.  
		On the other hand, I do think things need to change to where we're looking at all the evidence rather than just Phase III experience and ignoring the rest.  There is a concern that in the tougher areas that we begin to make development of new therapies almost impossible with the standard that we've had.  		We may push the drug development industry into areas that are easier to deal with when this is the number one cause of death and disability in the world and projected to be by even a bigger factor the number one cause of death and disability.  
		I've been involved in other committees now on several occasions in the last year and we have a tough standard of evidence than other committees.  Having said that, by our usual standard this doesn't make it even combining the studies.
		DR. KONSTAM:  Rob, I mean, it seems to me that your concerns ought to be held off until the end of the day because I think, you know, we're going to get into the fact that the problem is here we've got an act of control.  
		I think the question that Milton is asking us is simply do the data clearly demonstrate to us that we have a drug that's better than heparin.  That is the question.  I'm not sure that the answer to that based on rigorous statistical criteria is going to result in any kind of indictment of the process.
		DR. PACKER:  Okay.  Marv, why don't you begin.  Yes or no?
		DR. KONSTAM:  On this question?
		DR. PACKER:  On this question.
		DR. KONSTAM:  We have basically a single pivotal trial with a p-value of .08 on its primary endpoint so I think you have to start there and I don't know how you can really make that any better.  I would say no.
		DR. GRABOYS:  I say yes.
		DR. GRINES:  I would say yes but not to the primary endpoint.  I think again that this is one of these situations in the unstable angina trials where the company may have selected a different endpoint than some of the other drugs we approved.  If you look at the secondary endpoint, the triple endpoint, I think it's clearly superior to heparin.
		DR. PACKER:  Let me just make sure.  Tom, you said yes.  Cindy, you said yes.  Is that correct?
		DR. GRINES:  Correct.
		DR. PACKER:  Okay.  Tom.
		DR. FLEMING:  It is true that this assessment certainly needs to look at the benefit and the risk in the context of risk.  If we look at what are the measures that the sponsor is focusing on, which is the double endpoint and the triple endpoint, the OASIS-1 trial is not significant on these measures at day 7 or at day 35.  The OASIS-2 trial also is not.
		There is, in fact, a non-trivial, as we will be discussing later, excess in bleeds and major bleeds.  My assessment of benefit to risk, jumping ahead not having thoroughly had the risk data presented to us, is that these data don't establish superiority.
		DR. ARMSTRONG:  No.
		DR. LINDENFELD:  No, I don't believe they clearly established superiority.
		DR. PACKER:  Jeff has voted no.  Rob.
		DR. CALIFF:  A very reluctant no based on our standard.
		DR. PIÑA:  No.
		DR. DIMARCO:  No.
		DR. PACKER:  And my vote is no.  That's one, two, three, four, five, six, seven, eight, nine to two.  Okay.  Which brings us to the next part of the presentation which we will do after the lunch break.  We will take a 45 minute break and reconvene at about 20 minutes after 1:00.
		(Whereupon, off the record at 12:38 p.m. for lunch to reconvene at 1:20 p.m.)

A-F-T-E-R-N-O-O-N  S-E-S-S-I-O-N
1:28 p.m.
		DR. PACKER:  Can I ask everyone to take their seats, please.  It is going to be very important for this -- it is going to be very important for this committee to complete its deliberations in a timely manner today because many members of the committee have flight commitments and we will do everything in our power to retain a quorum of this committee.  Some who will be unable to stay until the final votes have already provided me with their votes on the questions that are in front of the committee.  That's not so unusual.
		DR. FISHER:  So I should sit down.
		DR. PACKER:  No, no, Lloyd.  You have most of us here.  We'll begin the presentation after the lunch break now with Lloyd Fisher.
		DR. FISHER:  I was going to open thanking the FDA for making me at home by bringing the Seattle weather but I made the mistake of going out at lunch and there was a strange ball in the sky so I won't make that remark.
		You have already heard the primary evidence comparing lepirudin plus aspirin to heparin plus aspirin.  However, the U.S. drug regulations are by in large written using the concept that an effective drug should be able to beat a placebo.  In situations where placebos are not considered ethical we do the best we can which is to estimate the effect of what might have happened versus placebo.  
		What we will do here is we will not only use the OASIS data but we will try to put it into context by looking at how heparin plus aspirin tends to compare to aspirin and then combining the two.
		Here is an outline of my talk.  I'm going to use the odds ratio as a measurement of treatment effect and I will explain to you why I prefer the odds ratio.  We'll talk about the selection of the randomized clinical trial data we want to use to estimate the heparin plus aspirin versus aspirin effect.  
		Then I will put that together in the putative placebo analysis, first for OASIS-2 and then for OASIS-1.  Finally I'll combine them with your permission.  If you want, I can skip the third slide.  I think the issue will be clear before that.  Then I will tell you the conclusions that I have from these data.
		Epidemiologists in general and people doing meta-analyses prefer odds ratios to absolute measures of treatment effect for a very good reason and the reason is empirically it tends to be much more stable across different studies.  That is, of course, immediately obvious if you had a fixed percentage of 
-- if you have a fixed odds ratio, then the absolute delta depends very much upon the proportion of the events you observed.
		In addition, there are theoretical reasons that suggest why this might be true.  I'm not going to mention that in the interest of time but Professor Gary Koch, who is here, and is published on this, the reference on the screen, would be happy to speak to this after the talk if you prefer.
		Let's move down to the second bullet here and this is the primary point to be made.  The OASIS trials, of course, had only two arms and I'm going to forget the fact that aspirin is in there because everything will be on top of aspirin, lepirudin and heparin.
		Suppose for the moment contrary to the facts that a placebo arm had been ethical and was in the trial.  Then it's a simple mathematical identity and easy to demonstrate that the odds ratio for lepirudin to placebo is equal to the product of two terms, lepirudin to heparin odds ratio and the heparin to placebo odds ratio.
		Now, from the OASIS trial or trials we have this odds ratio directly from the data you have already looked at and talked about considerably.  What we will do now is look at what data are available which might allow us estimate the odds ratio for heparin to a placebo for heparin all on top of aspirin.  The idea is the following.  
		We estimate the first term in this product from the OASIS trials.  We estimate the second term from previous controlled randomized clinical trial data.  When we have those two estimates, we can estimate the combined effect and put them together.  		At least as important as estimating the combined effect is if one is willing to make the assumption, and it is an assumption and I'm sure you'll hear about it from the FDA shortly because I was talking to some of them at lunch, but if you make the assumption that the odds ratio is transportable, if there had been a placebo arm in OASIS that odds ratio would be the same, then we can come up with mathematically appropriate confidence intervals, p-values, and so on.	
		The selection of the heparin plus aspirin data is described very briefly here.  We have a number of backup slides we can get into if you would like, the characteristics of the people in the difference studies and so on.  Most of the work was initially done by Oler in a meta-analysis published in 1996 in JAMA.  		The endpoint that he had that was closest to the endpoint in the OASIS studies was all-cause mortality or new MI.  I'm going to use that because that was the endpoint that was uniformly available across the studies.  I might also mention I think this endpoint is actually more appropriate because it's certainly a more meaningful thing to the patient than studying an only-cause specific endpoint.
		Because of the length of time that had transpired between Oler's meta-analysis, a MEDLINE search was performed to look for additional randomized studies involved heparin or aspirin or both and really not much had been done, although dalteparin had been compared both to aspirin and also to heparin.  
		And using the same methodology that I'm going to use to put together the putative placebo data, one can get an estimate of the aspirin versus heparin plus aspirin effect by combining these two studies.  You might ask why would one combine these two studies.  There's a variety of reasons.  One is these studies are the closest in time to the OASIS studies that are being talked about here.  
		Therefore, one would expect concomitant therapy and so on to be a little more contemporary and relevant.  Also, as a general statistical principle, I like to use the maximum amount of information.  Finally, I first became aware of this possibility from some other sponsor who presented me with the fact that these studies existed and they said, Is it appropriate to combine them?" 
		They didn't tell me what the data was or give me a clue to what was going on.  I said yes, and especially in this area where there is so little information it's appropriate to combine them.  The reason I bring that up is it will turn out these data give a very favorable, although not out of line, estimate of the heparin effect.  
		People tend to think of we statisticians as totally objective and computers.  Well, I can assure you we're not.  A lot of the subtle issues that come up on this committee, it helps to have a standard of the way you behave with respect to things, to know how you analyze the data, what you would do.  This was a decision that I made prior to myself being unblinded to the dalteparin data.
		One other issue which we've heard discussed today is what level of proof might one expect against a placebo.  Dr. Packer claimed that if there was a statically significant difference with heparin, I would submit that wouldn't have been true.  Number one, Rob Califf said people use .05 squared divided by 2 but that's in a placebo controlled setting without a serious irreversible endpoint.
		Historically with serious irreversible endpoints one study at .05 has been sufficient.  However, because of recent events people would like to see more evidence.  As far as I know, there is no agency-wide position on how much evidence.  I think it is fair to say that when people come in with a serious irreversible endpoint in one study, that they are often requested to have power for more than a significant level of .05.
		This is the first of a series of three build-up slides so let me orient you to this.  What we have here are the two sources of data I mentioned; the Oler meta-analysis, which is a combination of six fairly small studies.  It was not statistically significant as you can see from the fact that the odds ratio crosses the line at one.  That was published and is often sites as the reason the medical community started using heparin and to this day there is a very strong belief, as far as I can see, in the value of heparin in the setting.  
		The FRIC and FRISC combined actually.  Just this study standing alone has a statistically significant estimated odds ratio for the heparin versus placebo effect and arguably gives you more evidence that heparin is effective and the entire Oler meta-analysis thus justifying what the physicians have been doing anyway.  My preferred approach is --
		DR. CALIFF:  Lloyd, I hate to interrupt you but I want to be sure that we're clear on what FRIC and FRISC were actually comparing.  My understanding is one of them is actually low-molecular weight heparin versus placebo.
		DR. FISHER:  No, the dalteparin is a low-molecular weight heparin and it was compared to unfractionated heparin.  The estimate I have come up with -- thank you.  This was in my notes and I forgot -- is for unfractionated heparin versus placebo.  That's why two studies had to be used.  
		DR. CALIFF:  This is an indirect comparison?
		DR. FISHER:  Yes, this is indirect comparison of unfractionated heparin versus placebo.  This odds ratio is analog rhythmic scale for a variety of reasons, but perhaps the best reason is that an odds ratio of three is equivalent to an odds ratio of one if you took the treatments in the opposite direction.  As I mentioned, here we see evidence that heparin, in fact, is better than placebo when used in addition to aspirin.  
		What we have here are the data from OASIS-2.  We're talking about OASIS-2 up here for the endpoint of all-cause death plus new MI.  You can see this is not statistically significant, the p-value .086.  That is reflected in the fact that the confidence interval for the odds ratio just crosses 1.
		Now what we're going to do is to put the two parts together using not only the point estimates from the two parts but also the estimates of the variability from the two parts.
		This is my preferred estimate on the bottom that I will focus on because it uses all of the data.  I should mention FRIC plus FRISC looks a little out of line here but, in fact, of the six studies in the Oler meta-analysis two of the odds ratio estimates were .29 and .36 and this is .35 so it's not especially far out of line of the other data, although a lot of this is based on very small samples.
		The other thing I want to mention is on a log scale the confidence intervals are symmetric and you see some things that are not symmetric.  That is because we truncated the picture in order to enlarge things at an odds ratio of .25.  When you don't see the left-hand side, it's a conservative graphical approach in the following sense.  All I have done is thrown out values that are even more in favor of lepirudin than the ones that you see.
		Here we have if you use Oler alone, FRIC and FRISC or Oler plus FRIC and FRISC, an estimate granted based upon certain assumptions that had their been a placebo arm in the OASIS-2 trial, that the correct odds ratio, the best estimate is .49 with as confidence interval running from .32 to .75 with the small associated p-value that you have here.
		One thing you might notice is one could argue the case that there is adequate evidence for approval based on OASIS-2 alone just looking at this one slide.  That depends upon how robust you think findings have to be and a variety of other factors.
		Now what I'm going to do is to show you precisely the same figure both for OASIS-1 and the combination.  This is the same data from OASIS-1.  The first three lines, of course, are identical because we are using precisely the same control data.  In the middle of the slide you'll see the OASIS-1 data which for all-cause mortality and death is just right at statistical significance and the confidence interval just touches a value of 1.
		When we combine these you'll notice there's a missing circle on this thing.  The reason is this point estimate of .17 is even to the left of .25 so it's been truncated.  What you see here is the upper limit of that confidence interval.
		Again you can see there's a fairly low point estimate from OASIS-1.  As Tom and others have pointed out those data look for favorable and not surprisingly then you have a smaller estimated odds ratio, again small p-values.
		This finally is the combined data of -- I guess beauty is in the eye of the beholder -- either appropriately or inappropriately combined.  I'll just say it's consistent with the other two slides not surprisingly.  Actually, if you go back and look at the other two slides, this looks very much like OASIS-2 alone because, as you know, most of the data comes from OASIS-2.  The estimate rather than being .49 is .47 but it is essentially the same.
		I have done some other analyses which I will not present unless the panel requires it.  Rich Simon has a Bayesian approach using very conservative priors.  I have modified that for odds ratios and absolute treatment effects and have that prepared in backup if you would like to see it.
		I did an analysis on the percentage of the estimated heparin effect preserved by lepirudin.  All the point estimates, of course, are greater than 100 percent since things are close to statistical significance.  Of a variety of analyses the absolute worse thing I came up with was 95 percent confidence was that the lepirudin preserved at least 88 percent of the heparin effect.
		First, I conclude there is evidence, not as strong as one would like that, in fact, the use of heparin in acute coronary syndrome is not as off the wall as one might argue it could be if you're will to accept these sorts of assumptions.  That is statistically significant at the 05 level with FRIC and FRISC alone or with a combination.
		Lepirudin plus aspirin looks superior to aspirin with the associated confidence intervals and estimates of the odds ratios and p-values.  In my own mind these types of analyses, by the way, have been presented to this committee before.  It was presented for clopidogrel compared to the active-control aspirin.  A Bayesian analysis was presented for enoxaparin.  
		I think compared to the enoxaparin the inference here is at least as strong.  It's not as strong in some ways as clopidogrel because aspirin had been studied to a very large extent and there were literally tens of studies in almost any area you could think about.
		Given that, in my mind I also buttress this by several other things.  One, if you use a triple endpoint and you look at the medium dose, then actually both OASIS-1 and OASIS-2 individually are statistically significant.  The effect size that we see here, the OASIS data looked very much like other hirudin data from desirudin which Dr. Hirsh will be presenting shortly.  Let me stop here and ask for questions and/or comments.
		DR. PACKER:  We'll start with our primary reviewer, Dr. Borer, and then Dr. Fleming.
		DR. FLEMING:  Just a quick procedural question just also thinking of efficient use of time.  Is the FDA -- we've been given some handouts.  Did they intend to provide some comments on these issues?
		DR. PACKER:  Yes.  The sequence that we had envisioned was that we would lead with our primary reviewer, move to our primary statistical reviewer, and then move to the FDA statistical reviewer, and then have a discussion.
		DR. FLEMING:  In the interest of efficiency to avoid my overlapping what they're going to say, I'll defer my comments until after they present.
		DR. PACKER:  Okay.  Dr. Borer.
		DR. BORER:  Yes.  I want to preface what I'm going to say with the comment that I really don't think it's appropriate dealing with the issues with which we're dealing to be doctrinaire and rigid and all that kind of stuff.  I think that, Lloyd, you made the appropriate point.  We have to do the best that we can and there does have to be a way to develop new drugs.
		I also have to point out that virtually everything I know about putative placebo calculation I learned from you.  In fact, virtually everything I know about analyzing clinical trial data I learned from you. 
		DR. FISHER:  By the way, one other additional point I forgot to add is during the discussions with a consultant from the Cardio-Renal Division, Dr. Lipecky, so I don't pin this on GI, but he suggested -- not surprisingly because the history of this committee -- he suggested that putative placebo be looked at before OASIS-2 was unblinded.
		DR. BORER:  Okay.  Having said all those things, I need to ask a few things for my edification and probably for everyone else's except for Tom.  My understanding of the putative placebo construct that we have used in the past, or that we talked about and use sometimes, is that for optimal confidence one would like to have multiple trials showing quantitatively similar treatment effects of the comparator drug versus placebo.  Not just qualitatively similar but quantitatively similar.  That's what we'd like to have.
		I look at the Oler meta-analysis and it's true that the relative risk varies from .29 to .89.  the .29 is based on one event in 69 patients divided into two groups and on and on and on.  The point is that what we have here to make up that meta-analysis if you didn't just put the meta-analysis point up there but the individual trials including FRISC and whatever, FRIC and FRISC, is that we have multiple small trials on the Oler meta-analysis with a wide variance.  None was individually significant.  The meta-analysis for all of them together wasn't significant at the .05 level.  
		I don't want to misquote you but I think I learned this from you also at the meeting a couple of years ago about calcium channel blockers that for meta-analyses we generally expect a higher standard of proof; that is, .01 rather than .05 but we'll forget that for the moment.  		Then we added a different trial using --
		DR. FISHER:  By the way, Jeff, the standard of proof related to the final end of the thing, not the individual components.  If we had a billion small trials, I would be a lot happier obviously.
		DR. BORER:  Okay.  I know you would.  I'm just building up to a question here which is your comment.  Then we added another trial or pair of trials, FRIC and FRISC, that dealt with a different drug as a comparator for both of our drugs that we wanted to compare so we could compare a third drug to placebo and did some manipulations there.  That trial is far more impressive than really any of the comparators from the Oler meta-analysis and that really drives the significance of the subsequent meta-analysis including FRIC and FRISC.
		Then we are judging the effectiveness of lepirudin compared with that commish.  Now, I don't say that's wrong and it's probably the best we can do.  I may be sufficient to draw a conclusion.  But I'm concerned about the confidence that we can have in a putative placebo based on a number of very small trials with a wide variance, etc., etc., etc.  I would like you to comment about that.  Tell me where I've made my mistake here.
		DR. FISHER:  Well, No. 1, of course, I would be much happier, as would you be, if before this therapy was widely instituted the medical community had done what to me would have been the appropriate steps.  
		I guess I also have to say, and I hesitate to say this because one of the quotes I like is, "There's lies, damn lies, in statistics," in my clinical experience."  I have somehow gotten the feeling and I even had a line up here about biology and everybody jumped all over me.  
		It was perfectly clear to me I couldn't defend myself one biological iota so we took that off.  Given the consistency of all these interventions in this area and so on, I guess I have more belief in heparin than the meta-analysis indicates.  You have to insert your own judgment there.  
		I have more discomfort with this than I would had there been a number of larger studies.  This is the best that can be done.  Actually, in a lot of ways, I'm more comfortable in some ways with the dalteparin, FRIC and FRISC put together than the other studies to be perfectly frank rather than the other way around.
		As a general principle, as I've mentioned, unless I have a good reason to throw things out I go with maximum data and certainly there is not as much data here as one would like and I can't manufacture it.  All I can do is talk about what's there.  I have no magic answer to your concerns.
		DR. PACKER:  Could we ask the two FDA statistical reviewers to present their review of the putative placebo issue?  I think we'll begin with Dr. Permutt first.
		DR. PERMUTT:  Thank you.  I want to make a few general comments about this method as it is applied to the problem we have in hand.  Then Dr. Sue-Jane Wang, who has reviewed it in greater detail, I think has some more specific things to say.
		First of all, I heard both Dr. Fisher and Dr. Luz earlier refer to FDA regulations about the standard of approval being a comparison to placebo.  Now, I am not an expert in the code of federal regulations and I might be wrong but in connection with this very question, I have looked for that regulation and I can't find it.  
		I don't think there is any such regulation.  What there is in the code of federal regulations is a considerable discussion about the kinds of trials that might be considered to be adequate and well-controlled trials for the purpose of demonstrating what the law requires which is that the drug has the effect it purports or is represented to have.
		Now, one kind of trial that is discussed at some length is the historical control trial.  I think that is very relevant because that's what we have here.  When you are fairly convinced that you know what happens to people if they don't get your drug, then you don't even have to do randomized trials at all because you can do one-armed trials and find out what happens to people when they do get your drug and then compare that to what happened to people who don't get your drug.
		That's in the code of federal regulations but it's not used very much and we all know why it's not used.  It's because it is very difficult in general to say that what would happen to the patients in your trial if they hadn't got your drug is the same as what happened to patients in the past who haven't gotten your drug.  As Dr. Fisher said, the practice of medicine changes.  All kinds of things change from one population to another.
		What we have here is a version of a historical control trial.  We have an unsuccessful -- by its own light according to this protocol and the committee seemed to agree this morning, unsuccessful trial designed to demonstrate that Refludan is better than heparin.  
		Quite a large trial, one that if it had produced the expected effects would have been extremely significant.  		We also have some historical data comparing heparin to placebo in the presence of background therapy of aspirin.  
		As a member of the committee just remarked, maybe that's the best we can do here.  Maybe there is some way of inferring in our minds what the comparison of Refludan to placebo would have been.  		But to get to that to a p-value with three or four zeros on it and say you have actually compared Refludan to placebo and you know what the p-value is and so we have the equivalent of a placebo controlled trial so we're done I think is a very big leap.
		I think I'll leave it there unless there are questions and let Sue-Jane Wang tell you more.
		DR. PACKER:  Can we proceed to Dr. Wang's presentation.  
		(Whereupon, waiting for the machine to warm up.)
		DR. PACKER:  Is there any historical data as to how long this takes?  Are things in general going in the right direction?
		DR. FLEMING:  There is a trend.
		DR. LINDENFELD:  No statistical significance.
		DR. PACKER:  I have a feeling that the point estimate of delay has wide confidence intervals.  When I was in college I used to be a stand-up comic.
		DR. PIÑA:  Now, that makes sense.
		DR. KONSTAM:  Now you just sat down?
		DR. PIÑA:  It finally made sense.
		DR. PACKER:  It was a long time ago.  Maybe you can -
		DR. WANG:  I think the problem is I really need to show the graphics to explain what's going on.
		DR. PACKER:  The panel has the graphics.
		DR. WANG:  So I'll just be talking to the panel.
		DR. PACKER:  Okay.  Let me see.  Dr. Wang, we do have the -- I guess it's hard to discuss this in the absence of being able to point to the slides.
		DR. WANG:  If the graphics doesn't explain exactly what's going on, when is it appropriate, when is it not appropriate.
		DR. PACKER:  Does the committee have any other questions they want to ask, Dr. Fisher, while we're waiting?
		DR. CALIFF:  I certainly -- this FRIC and FRISC routine with no direct comparison between unfractionated heparin and placebo, how much confidence can we have in A is greater than B and B is greater than C.  Therefore, A is greater than C by some finite number.
		DR. FISHER:  Well, number one --
		DR. CALIFF:  I'm interested in Tom's point of view on this also.
		DR. FISHER:  Number one, the syllogism that A is equal to B and B is greater than C and A is greater than C is how it turns out.  Number two, the confidence went down because there were two studies.  The variances were added.  But the real concern that the agency has been speaking about is not that part of it because we statisticians can deal with that.  It's the --
		DR. CALIFF:  Wait.  Don't give me this we statistician stuff.  That's not acceptable to me.
		DR. FISHER:  No, no.  I was going to point out --
		DR. CALIFF:  You're telling me if you can deal with it that we never need to directly compare things.  We can always confer.
		DR. FISHER:  If you let me finish my statement, Rob, what I started to say is we statisticians can deal with that but the real issue is the assumption that this odds ratio would have been the same in both studies for the other thing that wasn't there.  That is definitely a big assumption.  		I'm in print as saying if you can ethically use a placebo, it's unethical not to use a placebo.  I don't literally mean that but you really should and I'm no big fan of historical controlled data and everybody who knows me knows that.  It's a situation what do we do where you're in an era where people ethically feel that they cannot use a placebo, that it has to be an active control.  So that's number one.  There is uncertainty there.  
		I don't believe, by the way, I ever claimed that the U.S. regulations said you had to use a placebo.  We can check the transcript when it's out but I said it was oriented towards placebos.  I do believe that is true and is correct.
		DR. CALIFF:  I work with a statistician who does what you just did and says it's just fine.  I'm interested in Tom's opinion as to whether adding the variances takes care of the uncertainty about the populations that were actually in the two trials.
		DR. FISHER:  No, it doesn't, because they are not randomized within the same trial.  You will never get exactly the same baseline characteristics.  Usually they are not totally contemporaneous in time, those two comparative trials.  There is additional uncertainty there that we statisticians do not have a good method to quantify.  It's up to your scientific judgment to decide how much that bothers you in this situation.  
		I am not going to stand up here and say we can just start using historical controls.  There is an infamous paper among statisticians in the New England Journal by Gehan Freidrich that got totally torpedoed from every possible side and appropriately so.  		What I'm saying is this is the best that I know how to do to evaluate this information.  It has weaknesses above and beyond the confidence intervals.
		DR. CALIFF:  My second question is did you do a sensitivity analysis on the overview to see what the least beneficial assumption for heparin could have been to still end up with a convincing p-value?  In other words, you're asking us to believe that heparin reduces the risk of events by 70 percent which is probably an over estimate most of us would think.  What if heparin only was half as good?
		DR. FISHER:  If you look at the confidence interval, of course, it goes up to 85 percent.  I'm looking at OASIS-1 plus OASIS -- no, that part remains the same.  I'm not asking you -- what I'm asking you to accept is basically a distribution of values centered around the point estimate but with the spread that I can account for statistically.  As I mentioned, for most of us the real concerns are not that part of it.  It's the assumptions that you have.
		DR. CALIFF:  But I'm driving at an issue here and I'm partly biding time but I think this is an important issue.  We can assume that what was reported in the early days on heparin versus control was highly selected for positive study.  
		It is much more likely of publishing a study now even if it's negative than there was 15 years ago.  What I'm really trying to get at is how much less impressive could heparin have been having still come to the same conclusion?
		DR. HIRSH:  As far as I know, no statistician has ever ventured a quantitative statement to that effect.  We have played around a little.  You saw some of the things that the agency reviewer did.  They said, "Gee, in FRIC and FRISC if we change data events this would happen."  You can play the same game the other way.  If we change it in the other direction, it really would have looked great.  I tend to like --
		DR. PACKER:  Sue-Jane, you're on. 
		DR. HIRSH:  -- to stand with the data that's there.  By the way, I did a few conservative things.  Oler looked at the end of treatment.  The end of treatment here is 72 hours where the data looks even better but I didn't want to do that because I thought it was fudging things.  
		Not fudging but it went in a favorable direction and the primary endpoint was at seven days so there are certain things I could have done but probably -- I mean, it would have made things look even better and I'm sure if I set my mind to it I could find things to do --
		DR. PACKER:  I think we're ready.  I think this thing finally came on.  Dr. Wang.
		DR. WANG:  Hi, everybody.
		DR. PACKER:  Speak up, Sue-Jane.
		DR. WANG:  Can you hear me?  Good.  All right.  I just like to make a point before I start.  I've been working in this area of research with an expert statistician from the FDA, Dr. James Hung, in the Cardio-Renal Division.  We actually had done a lot of work regarding this particular issue of putative placebo.  It just so happened here we have the application comes up and we can try to put these two things together to shed the light on what is going on in this particular NDA.
		I was called on to discuss this virtual method used in this particular reflected in the application.  As you know by now, it was because of one large multi-center double-blind control study of about 5,000 patients per arm might not have a statistically persuasive evidence and that was the pivotal study for evaluation.
		The virtual method used by the sponsor in the evaluation of the primary efficacy endpoint for the OASIS-2.  Here I like to explain this virtual method graphically.  First, let's focus on the left box.  This is the current active-control trial.  
		We have the experimental treatment and we have the active-control treatment.  If the estimated relative risk of the treatment over control and is 95 percent confidence interval limits are all less than 1, then treatment event rate is less than active-control event rate.
		In that case, treatment effectiveness would help establish and that's a check mark.  Due to the ethical reasoning, we may only be able to find some past trials in which the placebo arm was included for some time ago which is our right box.
		The external data or historical trial or placebo controlled trials are the term we used which generally consist of more than one trial.  If the effect or control relative to placebo can be ambiguously established, for example replication of the results, relative risk of the control to placebo and again is 95 percent confidence and everything being less than 1, then we have another check box there.
		Then the comparison of the treatment versus the placebo would be quite clear and straightforward.  Again, we have now the third check box.
		Now, the problem we're dealing with here is what if the results was a question mark on the left box and a question mark on the right box?  Can one legitimately evaluate the treatment versus placebo as shown in the box at the bottom?
		From our observation this is one of the objectives that the sponsors try to conclude.  The theme of the virtual method is to directly answer the question of treatment being superior to placebo, the bottom box, by making a few assumptions and by some statistical properties if used appropriately.
		So we have to talk about assumptions with this virtual method.  First, and the most critical assumption, is that effective control in the historical data is identical to the effective control in the active-control trial.  There is no sufficient data for verification of this assumption.  It is very difficult, if not impossible, to replicate the effect of control relative to placebo in a current active-control trial without the concurrent placebo arm.
		Secondly, for the mathematics to work out right, one needs to assume that the estimated relative risk of treatment relative to control obtained in the active-control trial is statistically independent from the estimated relative risk of the control relative to placebo gathered from potentially a few to many historical trials called meta-analysis.  It is assumed that the placebo control trials being included are clinically sounding and the statistical method for the meta-analysis used to estimate effective control is statistically valid.
		If all the above assumptions are met, then this virtual method can be efficient approach used to show that treatment is superior to placebo.  However, this virtual method can be very sensitive to departure from assumptions, especially if the effective control differed between the historical trials and the current active control trials.
		As I mentioned in the beginning,  progress this year has shown by simulation that when the control event rate in a current active-control trial increases just slightly compared to the control event rate in the historical placebo control trial, then the first positive rate of relatively concluding that treatment is superior to placebo can be large.
		From our simulation studies it appeared that the first positive rate can be very large in the number of trials available for random effect which was what the company used.  Meta-analysis is not large.  For example, even with ten trials the random effect meta-analysis can still carry a larger than expected false/positive rate.
		In fact, in Biometrics 1999 the title of that inference in random effect metal-analysis.  Follmann and Proschan from NIH also pointed out that when a number of trials is not large, random effect meta-analysis using normal approximation may not be valid for testing the effect of control relative to placebo.
		What we are seeing in this particular application, first let me focus on the Oler, et al., application.  As you know, the time is limited so my slides are actually cut into 1/3.  I hope I can make the story continue.
		I would like to here point out that the heparin plus aspirin, the active-control even rate, was not the same as that of the OASIS-2.  First of all, the heparin even rate was 4.2 percent from the OASIS-2 trial.
		If all the six trial estimate from the Oler study is used, the heparin plus aspirin even rate was 7.9 percent, the six studies there.  You can see that it was almost twice as high than that in OASIS-2.  On the other hand, when the three blinded trial estimate is used, the heparin plus aspirin even rate was now 2.2 percent.  These are the three blinded studies.  
		As far as application of the Oler six trials, it was shown that there were three blinded studies and three unblinded studies so here we show you when you pull together the blinded and if you just focus on the blinded results, you see that kind of difference.  Now with the three blinded studies the 2.2 percent is actually half that of the OASIS-2 estimate.
		So what does this tell us?  These raises the alarm that we may not yet have the effect of heparin plus aspirin clearly established and that assumption of the effect of control in the active control arm being the same as the effective control in the historical trial may be very questionable.
		Therefore, interpretation of comparison of Refludan with aspirin alone is highly dependent on selection of studies from meta-analysis.  Especially OASIS-2 did not conclusively reflecting being superior to heparin plus aspirin.
		As you can see from this slide, on the right-hand box when using the six trial, as the sponsor did, you would get a relative risk of .64 and that risk estimate with interval will be used to derive the relative risk of Refludan versus placebo of .56 leading to a significant Refludan effect of p-value .014.  
		However, if the three blinded trials are used, Dr. Rashid, the FDA reviewer, and also Dr. Hock in 1997 of essence trial review, both pointed out that the relative risk of heparin plus aspirin versus the aspirin alone would have .78 relative risk.  You can see the interval estimation now is much wider.
		When such an estimate obtained from the meta-analysis is used.  Relative risk of Refludan versus aspirin becomes .64 and that the p-value generated from Dr. Rashid and Dr. Hock was .095.  The .095 here could be underestimated.  When we actually perform the simulation study, based on the scenario observed from the data itself, we found that the false/positive rate was likely to be doubled around .18 in our research.
		The sponsor FRISC/FRIC study, there is actually a lot more story into it.  It is actually a two-step process in getting the control relative to placebo.  Since I have to skip a few slides, I hope I can explain better here.  The two-step process here that we're talking about is we don't have the middle to be the active control.  Here what we have is a D, the dalteparin, another treatment.
		For these two studies the trial have about 750 patients per arm.  One needs to be very careful in interpreting the result here.  Let's look at the right box of the FRISC study first.  This is just like the historical control trial we had before except that it is now placebo relative to treatment, not relative to active control.
		Dalteparin clearly was shown to be significantly better in reducing the risk of death or MI, p-value about .001 so we have a check here.  Dalteparin prevent rate was 1.8 percent in the FRISC trial.
		Now, let's look at the left box.  The FRIC trial served as the current active-control trial comparing heparin plus aspirin, the active control, to the dalteparin, the treatment.  This comparison would be valid if one could assume that the effect of dalteparin in the FRISC trial, which was 3.9 percent, is the same as that in the FRISC, 1.8 percent.
		If one perform a simple test for the statistical significant difference or no difference on this dalteparin, the p-value was .018.  This is exactly the situation we found from our simulation studies that false/positive rate of concluding that active-control is superior to the hypothetical placebo using such a virtual method can be very high.
		Now, move to the Oler trial.  As pointed out by Dr. Fisher in his manuscript, when the active-control trial show that treatment is superior to control and that the historical trial showed the control superior to placebo based on a large number of trials.  Then the population differences between the two type of trial will be of less concern.
		Here in this Refludan NDA we don't have convincing evidence of Refludan being superior to heparin plus aspirin in the active-control trial.  We don't have the convincing evidence of heparin plus aspirin being superior to the aspirin from just a few trials.  
		We do have differences among these small Oler at all trials.  Concerns of assumptions might not be met.  These are exactly the concerns that making the virtual comparison of Refludan versus aspirin alone difficult to conclude.
		In summary I like to convey a few important messages.  From the Oler et al. in addition to the dose regimen differences, definition of endpoint differences, trial design differences, small sizes of trials, number of trials which could be appropriately included for meta-analysis may be less than what is available.
		Here we had heparin plus aspirin event rate deferred from that of OASIS-2 between using the three-blinded-trials scenario versus using the six- trial scenario.  Therefore, the first key assumption for a statistical valid approach of virtual method may have been violated.
		Given all the uncertainty of the heparin plus aspirin effect seen in Oler et al. trials, should six or less than six trials be used for the meta-analysis especially the active-control trial seem to have a very weak evidence of concluding Refludan being superior to heparin plus aspirin.
		As you saw from earlier slides, with the FRISC and FRIC trial if conclusion of heparin plus aspirin being superior to placebo can only be 50 percent chance of being incorrect, one may have severely overestimated effect of heparin plus aspirin.  The question then becomes can such over estimate effect obtained from the FRISC/FRIC study be combined with Oler et al. trials.
		Finally, the virtual method can be very efficient but we found that it suffers from departure from key assumptions of control event rate being the same between the active-control trial and the placebo historical control trials.  Which, of course, we know could not be unequivocally assessed from existing trials.  The implication of this ought to be carefully considered, particularly in this NDA in which the active-control trial did not conclusively show Refludan is superior to heparin plus aspirin.  Thank you.
		DR. PACKER:  Dr. Fleming.
		DR. FLEMING:  Dr. Wang, while you're still here, in our briefing report from the FDA on page 34 it was suggested that the FRISC and FRIC trials data that we were using were from non-randomized arms.  Can you clarify what that is about?
		DR. WANG:  Okay.  I am not the reviewer for this NDA but my communication with the primary reviewer is that they are randomized studies.  Correct me if I'm wrong, Dr. Rashid.
 		DR. RASHID:  Yes.  FRISC and FRIC are randomized but we are comparing with the one arm from FRISC and the one arm from FRIC so there are two different arms of two different studies.  They are non-randomized.
		DR. FLEMING:  I see.  I'm going to try to be fairly brief here.  I'm acutely aware of time.  There are a number of issues and Dr. Wang has mentioned several.  As Lloyd Fisher pointed out, the critical challenge here is to be able to come up with studies that are going to be giving us a relevant estimate of what the active control's effect is.  
		We have been involved in active-control trials for a long, long time and I've always argued there are some critical ingredients required or assumptions or truths that have to be in place in order to be able to understand what the effect is of the intervention relative to placebo.  
		The first is the active comparator has to be a very effective regimen with a precisely estimated effect in the precise population in which the study is being done.  That also means concomitant meds, doses, other things, patient characteristics, things that could influence outcome need to be comparable.
		Admittedly to achieve that in the most satisfactory sense is an incredibly tall order and it's one of the reasons that active-control trials have been viewed to be less reliable in their interpretation than a direct placebo control assessment.
		A couple of things that I might want to turn attention to and they are somewhat related to Dr. Wang's presentation.  If we go to page 28, table 4.1. Lloyd might have a slide to this.  
		This, Lloyd, is the table that gives the six studies that go into the Oler meta-analysis.  The thing that strikes me at the beginning when I look at this is that the Holdright trial is dominating in terms of the number of events in this overview.  In fact, it's an event rate that is 27 percent on heparin/aspirin remembering that what we're looking at in OASIS-1 and OASIS-2 are event rates of 4.2 percent and 4.8 percent.  Presumably the Hold right analysis is looking at different time frame or different endpoint and Lloyd might clarify that while I go on here.
		The other five studies are on the opposite extreme.  They are very small studies with very low event rates so that you have a total of 13 events -- I assume these are death MI events from what Lloyd said -- 13 events on the heparin/aspirin and 28 events on the aspirin if you're looking at this meta-analysis without including the Holdright data.
		One of the first things that strikes me is that 13 events on heparin/aspirin gives you a 2.4 percent rate which is half of the event rate that we are seeing in OASIS-2.  The data are what they are but it's interesting that the event rate is low there for what we would expect it to be and it's these data that are the basis of our trying to estimate what the heparin effect is.
		It does raise for me one of the concerns, and we've already alluded to it, meta-analysis of the literature is what has been referenced as the way that Oler used to obtain these data.  These are very small studies and if you had a very small study of this size and things went in the wrong direction, interestingly none of these go in the wrong direction.  
		In such small studies that's probalistically unlikely that none of them would go in the wrong direction.  It just makes me wonder what else is out there that didn't get into the literature that is an equally small experience that as a result legitimately wouldn't be viewed to warrant publication.  Is this, in fact, an unbiased representation of the literature.
		Other issues that have been addressed, and I'll just be quick on these, is the endpoint is all-cause mortality and MI.  I actually agree with Lloyd.  I think that's the best.  It is slightly different from what we're using in the OASIS trials.  I think the Oler data is over the period of treatment and what isn't clear to me is if we can even say this represents the events in these five smaller trial that would have occurred up through day seven.  
		Of course, as I think has been made clear, I have reservations about whether just looking at effects over seven days is adequate.  There isn't evidence presented here to give us a sense of what was the effect of heparin.  How much of this effect was sustained out to day 35 much less day 180.  
		Concomitant meds, these could be different and Dr. Wang is referring to these issues and Lloyd has already alluded to them as well.  Issues that make one a little bit uncertain about whether these estimates are able to be translated into what we would have expected in the exact population that was in place for the OASIS-2 trial.
		The FRISC and FRIC studies if you turn to page 30 the data are presented there for these two studies.  What is evident here is the critical study here is the FRISC trial, not so much the FRIC trial.  The FRIC trial is telling us that dalteparin and heparin seem to be about the same.  
		The critical linkage to the placebo, so to speak, is the FRISC trial.  In this trial the estimated rate of events is also really low.  It's 1.8 compared to the FRIC trial where it's 3.9.  One is left with some uncertainties as well here.  You have very small numbers in FRISC.  You've got 49 total events.  
		I agree with whoever else made the comment.  The analysis of all of these meta-analyses for the putative placebo, the analysis that gives the most encouraging result is the FRISC/FRIC and it's really based on FRISC and FRISC is based on 49 events where you have an event rate in the dalteparin/aspirin group which is less than half of what you get in the FRIC trial.  
		In a sense we say this variability is factored in and Lloyd is right about that.  It is factored in because the methodology that he's talking about is, in fact, looking at if you want to compare A to C, you can look at A to B, B to D, D to C, and that gives you A to C and the variabilities are additive and they are factored in.
		When one looks at the data as to whether it makes sense, there are some of these issues that Dr. Wang had brought up come forward and certainly raise some concerns.  I guess ultimately one of the issues, too, that one has to think about, and it's a difficult philosophical issue, is the study was designed as a superiority trial.  
		It did not identify prospectively that it wasn't necessary to show superiority.  It was adequate to show non-inferiority via a specific margin or according to a specific method where we would be using given trials as a way of assessing the effect of the placebo against the active control.
		If you had set out to do an active-control trial to show non-inferiority and you actually established superiority, we all accept that as being a fully appropriate conclusion.  What is problematic is when you set out to show superiority and you fail to do so and then you acknowledge what may be true.  		It's not necessary to show superiority.  It's actually adequate to show non-inferiority, but then we're stepping back and using data.  That may be out best attempt to choose those appropriate historical experiences that will represent the effect of this active comparator.  
		There are going to be necessarily judgments as to which of these studies are appropriate and which are not.  It's very difficult when it's left with the sponsor to carry that judgment out because you know, in fact, what the results are going to be when you see these studies as you are deciding which of these studies to choose.
		Ideally, prospectively one would have an independent group of people surveying the literature without a specific interest, financial or professional interest choosing those studies that are the most reliable way of assessing what the effect of the active comparator is and proceeding forward.
		Of course, even in that ideal setting the studies that you may have to choose from may be limited in terms of the reliability that they are going to be able to provide for this assessment.
		My sense is that if the approach that Dr. Fisher has laid forward is methodologically very reasonable, the concern is what we can put into that approach, i.e., the trials that are available as the evidence that he is required to use in order to ultimately assess what the effect is of heparin.  In fact, if it were this clear, i.e., if it was widely accepted that heparin was effective, is it, in fact, not labeled in this indication?  It's an interesting philosophical issue in itself.
		DR. PACKER:  It's not but whether it would be labeled if an application were made is a separate issue.  Clearly the agency does not rule on applications that are not before it.
		DR. FLEMING:  So, in essence, the concerns that I have is as you look at the most critical elements of these studies that are the basis of determining the effect of heparin, if you look at the Oler study, the data in terms of numbers of events are dominated by the Holdright trial that is completely out of line for what the event rate ought to be.  
		The remaining studies are all incredibly slow and give an aggregate event rate that is less than half of that that we have seen in the OASIS-1 and OASIS-2.  Similar comments for FRISC which is the critical study for that particular.  Bottom line is we're looking at OASIS-2 at a study that provides 714 events that's the basis of our understanding what the effect is relative to heparin and we are relying on 49 events in the FRISC approach.  
		And we are relying on if you put aside Holdright 13 events plus 28 or 41 when we're using the Oler approach.  There's extreme concern about how reliable our estimates of heparin are with this approach.
		DR. PACKER:  Dr. Fisher.
		DR. FISHER:  I wanted to make a couple of comments.  It's always tempting to get into a debate mode but we are here basically to work on data.  First, I want to be sure I understand what the agency did.  Your false/positive rate of 50 percent, you said there was one underlying control rate?  Is that correct?  The simulations?  The reason I ask is unfortunately I've done this so recently it wasn't in the review document so it's a little hard to react in real time.
		DR. WANG:  The way we did the simulation study is to say here is the data that we observed.  Given this is the likelihood of the truth, then what would be the probability of saying that treatment is going to be superior to the placebo, the aspirin given that there really is no difference.  Yes, we do utilize the data information to try to simulate the data as it is.
		DR. FISHER:  I don't quite understand.  That means that the data would show the difference to say we simulate under the null hypothesis with the likelihood -- as I understood it, I'll only make one point that I think is a fallacy both addressed by the FDA and by Tom.  To me what they were going on and on about these rates and the trials is precisely -- precisely why people use odds ratios.
		If you look at the aspirin data, for example, that's how you get consistency.  You don't compare the rates in the trials.  You compare the odds ratios or the relative risk and that is very important because the populations are never quite the same and this is the one thing that makes totally using historical controls so difficult.
		DR. FLEMING:  There's no debate about using odds ratios.  I'm very comfortable with that.  If we go to page 28, if you have that slide, is it, in fact, true if you look at the Holdright data that we're looking at, an event rate of 27 percent?
		DR. FISHER:  I haven't computed the event rate but we can put up -- let me see if I find the -- why don't you put up slide LF-23.
		DR. FLEMING:  The debate isn't about whether the odds ratios --
		DR. FISHER:  Not the actual values.  The individual studies are behind you.  If you go to the next slide, there's a plot and, as you can see, the Holdright data is the majority of the data and the small studies have much wider confidence intervals.  That's why, of course, the relative risk is much closer to the Hold right data than a lot of the other data points.
		DR. FLEMING:  Lloyd, we want to make sure.  The issue at hand here isn't whether the Hold right is saying the relative risk is of the same order of magnitude as the other studies.  The issue is the Holdright data is based on what is hidden there, the fact that the baseline event rate in Holdright is, I believe, 27 percent.  In the aggregate of the other five studies, it's 2.4 percent.  Is that, in fact, true?  It is true.  And how is it 27 percent in the Holdright study?  Is that, in fact, death MI at day 3 to 7?
		DR. YUSUF:  None of this is death MI.
		DR. FLEMING:  That's not what Lloyd said.
		DR. FISHER:  Yeah, this is.  It is death MI.  
		DR. FLEMING:  It's certainly relevant to know.  We should be talking about the same endpoints over roughly the same time period in order to be able to use your method appropriately.
		DR. FISHER:  I can give you the time periods for the individual studies.  It was six days, five days, three to four, three to four, three to four, two and five to seven so about five to six days is the average whereas our endpoint was at seven days.  As I mentioned, I didn't go back to the end of therapy to make it more comparable because that was more favorable.
		DR. FLEMING:  Is there any explanation?  Is it surprising to anybody that we're seeing a 27 percent event rate?
		DR. YUSUF:  Tom, there's no explanation why the Holdright absolute event rates are different from the others.  Having said that, whenever we do meta-analysis in different areas there is a huge difference.
		The second thing is just the calculation you did, if you take out Holdright which is the outlier in that, you said it's 30 versus 28.  The odds ratios will be lower and the confidence limits will be tighter.  If Lloyd were to do the same calculations excluding Holdright, the effect sizes will be bigger and the p-values will be more extreme.  I'm sure the p-value of 0.06 will be well less than 0.05. In a sense what Lloyd has done is more conservative than if you take Holdright out.
		DR. FLEMING:  What we have -- and the committee can look at page 28 -- what we have are six studies.  There is not a single study in this group that provides a substantial amount of data with an event rate that is remotely close to what we are seeing in the OASIS trial.  I worry about the interpretability of what is base in Holdright.  I have serious concerns about how to interpret that, 27 percent in the heparin arm.
		If you pool the other five, the big concern that I have isn't that those are individually invalid.  They give us a totality of 13 events.  These are exactly the types of experiences that you would expect could readily have not been published.
		DR. FISHER:  But although there are other concerns as has been expressed, one can also make the argument fairly strongly based on FRIC plus FRISC alone throughout all of Oler.
		DR. FLEMING:  And the critical study there is FRISC because that's our linkage, what we are really crying out for here.
		DR. FISHER:  No, you're saying it's critical because that has the big non-one estimate.
		DR. FLEMING:  No, Lloyd.  It's because what ultimately we have to do is we have to get a comparator to ask for alone and that is what FRISC is providing.
		DR. YUSUF:  You raise two issues, Tom, which I would like to respond to.  The first is whether these trials are biased in any way.  That is a very hard one to answer but I can answer it.  We've done three things to look at it not because of this presentation, because we have a paper coming out in the Lancet where we've done a meta-analysis of all the unfractionated heparin trials and all the low-molecular weight heparin trials.  
		All we found was 100 more patients in the unfractionated heparin trials.  In doing this we wrote to everybody who did unfractionated heparin trials.  We wrote to every company that had unfractionated heparin.  We also wrote to the Cochran database.  We did as an exhaustive literature search as is humanly possible.  The second point I wanted to make --
		DR. FLEMING:  My concern is getting away from a literature search.
		DR. YUSUF:  That's why we wrote to people.  The companies that did the trials, the Cochran database, and people that we knew were interested in unstable angina asking them, "Do you know if a trial was missed?"  Several of you know that is the approach we take.  It takes years to do that but we really did that and we couldn't honor extra data.  This doesn't mean I can guarantee there aren't trials out there.  This just means we did the best humanly possible and it doesn't alter this.
		The second point is the event rates does not invalidate -- variable event rates in different trials does not invalidate the estimates that you derive from meta-analysis.  For instance, within a given trial, you can have low-risk patients with a one percent event rate and high-risk patients with a 10 percent event rate and you calculate an overall treatment effect because the odds ratios are transportable.
		DR. FLEMING:  That's what you have to assume.  You have to assume that the overall effective intervention is independent of many other factors that are strikingly influencing event rates.
		DR. YUSUF:  And where we have a lot of data, for instance, we have the data with beta blockers.  We have the data with aspirin.  We have the data with cholesterol lowering.  Lots of areas where you do have good data, that assumption --
		DR. FLEMING:  But we don't have the data with heparin.  You've just indicated we don't.  The critical question at hand here is heparin.  Is, heparin, in fact, providing a 10 percent, 20 percent, 40 percent reduction.  That's the question at hand.  Not aspirin, not anything else.
		DR. YUSUF:  Tom, I'm talking for general principle, the general principle being absolute event rates don't invalidate the meta-analysis or the estimates within the totality of a single trial because different subgroups can have different event rates.  We all agree we wish we had more data on infractionated heparin.  We are in this unfortunate situation, difficult situation, where clinicians are absolutely convinced that unfractionated heparin should be used.  We did pull 500 centers before we started this trial.  Can we do this trial with this placebo?  Unanimously not one center said we could do it versus placebo.  Whatever the reason, the people are convinced this works and the modest amount of data that there is, which is not ideal by any means, is what you have in front of you, and is supported.  
		DR. FLEMING:  What you're describing is, in fact, the very common and unfortunate but classical limitation that we encounter as we attempt to do putative placebo assessments.  It's exactly as you say.  Very often we're in this circumstance.
		DR. YUSUF:  Tom --
		DR. FLEMING:  The fact that there are, in fact, no other data doesn't, though, allow us to say the data that are here are more reliable than they otherwise would be.  The critical limitation of a putative placebo argument is that you've got to come up with an estimate that is reliably predicting what the effect of that putative placebo would be in the population and if you see an event rate that is five-fold or eight-fold larger than in your trial, it's immediately clear that the circumstances of the other trial are very different.  You are having to assume that the odds ratio effect of heparin in that setting would be like what you have no data on which is the odds ratio in your setting for the effect of heparin.
		DR. YUSUF:  That is an assumption that we have to make like a tautology.  One little point, Tom, just to point out.  It's the page 28 table you pointed out.  Holdright had an unusually high event rate but that is a trial that showed the least treatment effect.  We took the rest of the data, the number of events of 13 versus 20, on approximately similar numbers of similar people in the autumn group.  		Yes, you immediately point out they are tiny numbers but that's all we have.
		DR. FLEMING:  Tiny numbers and now with a very low event rate lower than the OASIS trials.
		DR. YUSUF:  Yes, but, you see, we agreed in principle the event rate does not effect the treatment effect size across most treatments that we've been able to examine.
		DR. PACKER:  Let me try to do the following.  I think that the committee has heard and understands fully well what the issues are and it is unlikely that we will be enlightened further by discussions on this issue.  What I would like to do is ask Dr. O'Neill for his comments on it because that would be, I think, helpful to our deliberations.
		DR. O'NEILL:  I think what you've heard over the last hour, hour and a half, is a discussion of a method that Lloyd Fisher has proposed for imputing a placebo.  There are two aspects to that method.  One is relying on meta-analyses and various strategies for the meta-analyses which includes which studies go into those meta-analyses.  
		I think you've heard from Tom Fleming that there is a concern that there is a fair amount of heterogeneity in sample size as well as background event rates among those studies.  How they all got in there is your guess.  They are from the literature and it's well known that lots of studies don't get into the literature.  If you are negative, you don't get into the literature.  That's the point Tom was trying to make.
		The other point is the fact that the imputation strategy separate from the meta-analyses has an extremely strong assumption.  What you've heard from Sue-Jane Wang is an effort that has been going on at the FDA ever since the "imputed placebo strategy" has been thought about to deal with what is a tough problem.  We have a lot of concerns that no one has gotten it right yet.  
		In this particular instance this method hasn't gotten it right is an extremely strong assumption.  The assumption is that everything is the same and would be the same in this current study as it was in "the historical meta-analyses trials."  I think it's pretty apparent that Tom Fleming has pointed out that there is a lot of differences in heterogeneity in the studies.  That's the bottom line.  
		Sue-Jane has said when there is heterogeneity, you're false/positive rate is very high.  So the issue then is you can't believe any of these p-values that you've been seeing.  They can be inflated dramatically.  How much we don't know but this is very early in the first and second stages of what I would call this imputed placebo strategy effort.  
		We're in the second inning of a nine-inning game.  This is a methodology that is being proposed and there are so many unknowns.  There are more questions than answers.  To make a major decision on the basis of this, that's not to say that it's not a worthwhile effort but there are a lot of things that I think have been pointed out that empirically justify the concerns.  
		You need to think about why people are analyzing in the literature heterogeneity and meta-analyses.  They take the very simplistic approach.  While Salim might say that the treatment effect is independent of the control rate, I don't think so.  		There's a lot of effort around in meta-analyses which show that your treatment response is related to what your background event rate is.  We've seen in this collection of the three studies of the Older meta-analyses or even within the context of the OASIS-1 and OASIS-2 so differences in the event rates.  		What Sue-Jane Wang was saying is the inference on this imputation strategy is extremely sensitive to that.  I think empirically there is enough evidence for that.  FDA had done a little more than was presented and, in the interest of time, not all the slides were gone through.  
		You have to realize this is tough sledding.  This is not simple stuff.  The material that Lloyd Fisher presented in the application needs a lot of thought.  We put a fair amount of thought into it and we have a lot of concerns and I think you have seen part of the concerns from Sue-Jane Wang and that's what the bottom line is.
		DR. PACKER:  Dr. Koch, we'll ask you to respond.  Please, we are desperate for time so we'll ask you to be to the point.
		DR. KOCH:  Yes, I will be to the point.  It's responsive to something that Dr. Califf asked.  He asked whether there were any sensitivity analyses done.  Yes, there were sensitivity analyses done but they were done by a different method.  They were done by basically asking the question that had aspirin been the control group in the OASIS-2 study, what is a reasonable number to expect as the additional number of people with death or MI in OASIS-2.
		To do that we assumed different values of relative risk for heparin versus aspirin.  The conservative estimate that we used was in the vicinity of .8 top .85 at the higher end of the confidence limits that Dr. Fisher showed.
		We also made the assumption that anybody who had a failure on heparin would have also failed on aspirin as well.  We then used the event rate on heparin to estimate a conditional probability of failing on aspirin given that you did not fail on heparin.  We used a lower-bound confidence interval on the heparin rate when we did that. 
		We also calculated a lower-bound on the number of additional aspirin type patients who would have failed had aspirin been the comparator.  It would have been at least 25 to 35 and p-values that you get when you do that are below 01.
		Obviously, if you make stronger assumptions about how good heparin is, the results get stronger and this methodology can be shared with the FDA if there is an interest in this as an alternative approach.  It was mainly done to simply verify the kinds of information that we were getting from the meta-analysis and the putative placebo analysis that Dr. Fisher presented.
		DR. PACKER:  Marv, quickly.
		DR. KONSTAM:  Well, I was just going to ask about the sensitivity analysis because I think the situation that we're in is that the community is practicing in a way that is not condoned by the FDA.  The data that's been shown to us I gather represents the entirety of data upon which we can estimate the degree to which heparin, in fact, is acting.  With all the caveats of the problems with that data, I think it helps me in figuring out how I'm going to come down on this to really see what our point estimate of heparin effect is influences the value of our drugs.  I don't know if it's worth showing a slide of that.
		DR. PACKER:  I have to take the chairman's prerogative and simply say that there is a sensitivity analysis in the documents which have been presented to us.  Is that not correct?
		DR. KONSTAM:  No.  We haven't seen a slide of it.
		DR. PACKER:  Oh, we haven't seen a slide of it.
		DR. KOCH:  There is a slide that the sponsor prepared with a somewhat different kind of sensitivity analysis.  What I described was a different way of doing the sensitivity analysis that I did independently which shows basically the same thing.  
		The point is if you're willing to accept on the basis of what you saw from FRISC/FRIC and Oler that a reasonably conservative estimate of the relative benefit from heparin is a risk ratio of .8 moving up towards .85, then there's different ways in which you can combine that with the OASIS-2 study to produce p-values that start moving down below 01 and you just have to decide.
		DR. KONSTAM:  In fact, Gary, you've already got it.  It's in the OASIS-2 analysis.  Basically just look at the confidence interval for the relative risk and see and inferiority analysis if it excludes what you consider to be where the placebo would reside.
		DR. KOCH:  Yes.  Or if you're interested in the superiority to aspirin, you simply multiply the confidence interval by .8 on both sides.
		DR. PACKER:  Marv, I just want to clarify one thing.  I don't think that the FDA takes any specific position on the efficacy of heparin so that it's not that physicians are practicing or not practicing the way which the agency would condone.
		DR. KONSTAM:  All I said is it's not condoned.  In other words, the FDA has not indicated that it's effective therapy.
		DR. PACKER:  I think that the only thing that one can do is take the data that exist with heparin and we have seen that data presented.  The limitations of the analyses that have been presented have already been described by many individuals.  
		It is the only data that exist and the question that we need to address and in part intuitively is whether the limitations which are known to accompany the kind of analyses are of sufficient concern to us that they would weaken an argument that lepirudin is effective had it been compared to placebo.  In other words, the limitations that are -- I think, Lloyd, you agree with the limitations which have been presented.  Is that correct?
		DR. FISHER:  Yes, yes.  None of us can generate more data or data that were acquired other than how it was.  That is certainly true.
		DR. PACKER:  I can see actually no philosophical or mathematically important differences in the two views which have been presented.  It is really up to us to determine whether the assumptions which are inherent in the method that Lloyd has presented are of sufficient concern to us to effect conclusions regarding the efficacy of lepirudin versus placebo. Is that fair?
		DR. FISHER:  In that the estimated magnitude of the estimates are so far off.  I'll mention briefly what I mentioned before.  Behind you on the screen, the estimation of the percent of the estimated heparin effect preserve with the confidence intervals.  
		This doesn't directly affect that but you can mentally slide things down quite a bit and you'll still look good relative to the estimate of heparin.
Now, you have to decide if that heparin estimate has any validity or, in your own mind, what you think is going on.
		DR. PACKER:  We are not going to become smarter.  
		Tom, you're going to get the last word.  		There is no mechanism of becoming smarter today.  The data that we have are the only data we have and the assumptions that are inherent in the model have been described and outlined and agreed to by all concerned.  Tom.
		DR. FLEMING:  I'm just concerned that we haven't discussed safety.
		DR. PACKER:  We're going to do that right now.  Can we present safety, please?
		DR. LUZ:  Since patients treated with antithrombotic agents are known to be at increased risk of suffering hemorrhagic adverse events -- sorry, I missed that slide.  My talk will be structured as follows.  First, I will give you an overview of the safety data collected and the definitions used in the OASIS studies before I turn on to discuss the individual findings for bleeds, strokes, and other adverse events.
		Due to the known increased risk of bleeding in patients treated with antithrombotics, the key focus of the safety evaluation in the OASIS studies has been on the occurrence of minor and major bleeding events.  
		A second focus has been on the occurrence of stroke.  In particular, hemorrhagic stroke.  Both major bleeds and strokes were essentially adjudicated by the blinded adjudication committees of the studies.
		Consistent with the short half-life of the drug and the short duration of treatment in the trials, the focus of both the safety evaluation and this presentation will be on the initial seven-day period.
		The OASIS study protocols prospectively define major and minor bleeds.  According to these definitions, major bleeds were all those bleeds that were fatal, life-threatening in the opinion of the investigator, bleeds that required surgery or transfusion of at least two units of blood or blood products, or those that again in the opinion of the investigator were permanently or significantly disabling.  Minor bleeds were all those that were not major.
		Before CCC, the coordinating office of the trial in Hamilton and blinded the study, they recognized that in a number of cases investigators had specified life-threatening as the only criterion of major bleed without any objective evidence to support this classification.
		In particular, many of these bleeds were not fatal, not intracranial, nor did they require surgery or transfusion.  Therefore, for the analyses CCC introduced a new objective definition of life-threatening bleeds.  That includes all bleeds that are fatal, intracranial, required surgery, or transfusion of at least four units of blood or blood products.
This definition has been adopted by Aventis for our own analyses.
		Stroke was defined in the OASIS study protocols as the presence of new focus neurological deficit thought to be vascular in origin with signs or symptoms lasting more than 24 hours.  Three types of stroke were differentiated; hemorrhagic stroke, ischemic stroke, and stroke of uncertain type.
		Importantly in the analyses of bleeds, both hemorrhagic and uncertain stokes were counted as intracranial bleeds in order to avoid any potential underestimation of the frequency of intracranial bleeds.
		I will now turn to discuss the bleed findings first from OASIS-1 and then from OASIS-2.  This slide gives you the most important bleeding findings from the OASIS-1 study.  As you can see on the left-hand side of the slide, there was a clear and dose dependent increase in the rate of minor bleeds from 10.6 percent in the heparin group to 16.3 percent in the low-dose lepirudin group, and 21.5 percent in the medium-dose lepirudin group.
		In contrast, there was no difference in the occurrence of major bleeds and the absolute rates of major bleeds were low in all three treatment groups.  This is also reflected if one looks at the subcategories of nonlife-threatening and life-threatening major bleeds which all occurred at low and similar frequencies in all three treatment groups.
		This is the same presentation for the OASIS-2 study.  Again, there was a highly significant increase in the rate of minor bleeds from 4.5 percent to 7.7 percent.  You will note, though, that the absolute incidences were much lower than in the OASIS-1 study.
		Although there was a similar relative increase in the incidents of major bleeds that also reached the level of statistical significance, the absolute rates of major bleeds were low and, in fact, as low as in the OASIS-1 study.  
		As you can see on the right-hand side in the right half of the slide, the entire difference in major bleeds was accounted for by nonlife-threatening major bleeds but occurred at a frequency of .3 percent in the heparin group and .8 percent in the lepirudin group.
		In contrast, there was no difference between the groups in the occurrence of life-threatening bleeds but were observed at a frequency of .4 percent in both groups.
		This is a break-down of major bleeds at seven days by the categories that were provided in the data collection forms.  As you will note, the incidences of fatal bleeds, intracranial bleeds, and bleeds that required surgery were, in fact, low and similar in both groups.  Of note, among the five intracranial bleeds, there were four uncertain strokes and only one confirmed intracranial bleed that was observed in the heparin group.
		Most of the major bleeds were managed with transfusions of at least two units of blood and there was a statistically significant difference between the groups with the higher incidents observed in the lepirudin group.
		Similarly, there were appreciable differences between the groups in the occurrence of bleedings that in the opinion of the investigator were permanently or significantly disabling or life-threatening.
		Looking at the leading sources or locations of bleeds, you will note that the leading sources that also accounted for most of the difference between the two groups were gastrointestinal and hematuria.  The relatively low rates of surgical and puncture site related bleeds should be interpreted on the background of the relatively low intervention rate during the infusion.

		Among the other major bleeds that are not further specified here, there is a total of three retroperitoneal bleeds, two in the heparin group, one in the lepirudin group, and no intraocular bleed.
		With respect to minor bleeds, the leading source was puncture site related bleeds.  Here there was no difference or the incidents were similar between the two groups.  Across the vast majority of all other sources of minor bleeds the overall pattern that showed an increased risk of minor bleeds in the overall population was also reflected in the subgroups.
		We also performed a substantial site of subgroup analyses that were all prespecified in the statistical analysis plan.  The subgroup analyses were done on hemorrhagic adverse events as opposed to bleedings.  Hemorrhagic adverse events included obviously all bleeding events but in addition also events that were not bleedings themselves but associated with a certain risk of bleeding.  In particular, false vascular aneurysms.
		Over all the pattern of hemorrhagic adverse events across the subgroups was reflective of the overall pattern in the total study population.  There were, however, two subgroups with disproportionately increased rates of hemorrhagic adverse events, namely patients with a baseline creatinine of more than 1.5 milligrams per deciliter and patients weighing less than 50 kilograms.
		These are the findings.  As you will see, while there was no appreciable difference in the incidence of hemorrhagic adverse events in the heparin group between the subgroup levels for baseline creatinine, lepirudin patients with a high baseline creatinine had, in fact, a disproportionately high rate of hemorrhagic adverse events.
		The same observation can be made for weight where there were only minor differences for heparin but, again, a disproportionately high rate in lepirudin patients weighing less than 50 kilograms.
		As I pointed out earlier today, patients were to be excluded from participation in the trial if they had renal insufficiency as assessed by a creatinine level of at least 2.0 milligrams per deciliter.  If at any point during study infusion elevated creatinine levels were found, the infusion dose was to be reduced by 50 percent starting at levels of 2.0 and to be terminated with levels exceeding 2.5 milligrams per deciliter.
		There was no weight adjustment below 50 kilograms in the trial so the adjustment was only made in the range between 50 and 100 kilograms.  Based on the subgroup findings that I just presented, we now conclude that obviously a dose adjustment would be needed in patients with elevated baseline creatinine starting at a level of 1.5 milligrams per deciliter and the weight adjustment should cover the entire weight range including low body weights.
		We've also investigated the potential impact of warfarin, indirectly assessed the impact of warfarin on the overall study results.  You've seen a similar presentation in Dr. Yusuf's talk.  This is a comparison of the overall study results with the results in patients who did not receive warfarin.
First for minor bleeds in the top half of the part and then for major bleeds in the bottom part of the slide.

		As you can see, the difference in the risk ratios was, in fact, very moderate with the 95 percent confidence intervals overlapping widely.  At least the data would indicate that the additional warfarin did not substantially increase the risk of bleeding in lepirudin patients.
		Beyond seven days both in the period between eight and 35 days and 36 to 180 days the extent of bleeding was considerably lower than during the first seven days and there were no appreciable differences between the groups in any of these two periods.
		In the following I will be discussing the stroke findings again starting with OASIS-1 and then moving on to OASIS-2.  These are the stroke findings from OASIS-1 at seven days on the left-hand side and 35 days on the right-hand side.  You will note that the number of strokes and the incidences were very low and there were no differences between the treatment groups.
		In OASIS-2 at seven days the overall stroke rates were relatively low and almost identical in both groups.  Similarly, there were no differences in the occurrence of hemorrhagic stroke, ischemic stroke, and stroke of uncertain type.  Importantly, there was no single hemorrhagic stroke in the lepirudin group in both OASIS studies during the first critical seven days.
		At 35 days there was a slight imbalance in the overall stroke rate between the two groups with a slightly more strokes observed in the lepirudin group.  The difference did not reach the level of statistical significance though.  However, there were contrasting effects on subcategories of stroke that I will explain to you in the following.
		Hemorrhagic strokes were observed less frequently in the lepirudin group than in the heparin group, the difference being statistically significant.  Similarly, ischemic strokes were observed more frequently in the lepirudin group than in the heparin group, and again there was a statistical significance associated with the difference.
		These findings are currently unexplained given that in the period beyond seven days there was no difference between the treatment groups in other hemorrhagic events, and given that during the same period there was no difference between the groups in the occurrence of other ischemic events, namely cardiac ischemic events.  It is difficult to explain these findings.
		If one compares the findings for ischemic stroke from the OASIS-2 study with literature reported data that are available from the GUSTO-IIb study looking only at patients who did not present with ST elevation at baseline and the PURSUIT study, it becomes clear that the .7 percent rate of ischemic stroke observed in the OASIS-2 study is consistent with the findings from these other studies.
		In contrast, the .3 percent rate observed in the heparin group of the OASIS-2 study is surprisingly low against the background of the literature reported data.
		In the following I will very briefly discuss the findings for other adverse events.  This is just a summary slide indicating that there were no differences in nonhemorrhagic events at seven days between the two treatment groups and for serious nonhemorrhagic adverse events.  If anything, the rate was slightly lower in the lepirudin group than in the heparin group.
		Reassuringly given that lepirudin is a heterologous protein, there were no differences between the groups in nonserious or even serious allergic reactions.
		In summary, at seven days there was excess in minor and nonlife-threatening clinically manageable major bleeds in the lepirudin group.  There were no differences in life-threatening bleeds, no difference in stroke, and no difference in the occurrence of other adverse events.
		At 35 days there was again no or only a slight difference in the occurrence of total stroke.  However, there were contrasting effects on subcategories of stroke that occur in the unexplained.  There were no differences in the occurrence of other adverse events at that time point.  Thank you for your attention.
		DR. PACKER:  We'll begin questions with our primary reviewer, Dr. Borer.
		DR. BORER:  You had approximately just slightly less than, I guess, 100 patients in each arm of the study who underwent coronary artery bypass grafting after the infusion was begun -- after either infusion was begun so there are about 200 patients total.  I don't know how many of those patients were operated on within 24 hours of cessation of the infusion.  I would like to know that.
		Then I would like to know what the perioperative mortality rates were in the patients who were on lepirudin versus on heparin, the whole group or the 100 versus 100, and for those who are operated on within 24 hours of stopping the infusion.  I would like to know the blood products used in those two groups as well.
		I would like to know how many patients were brought back to the operating room for bleeding.  Not complication but for a post-op bleeding in the two groups, if you can compare them.
		DR. LUZ:  Let me start with the last part of your question.  As you saw in the breakdown of sources of major bleeding, there were only eight versus seven surgical bleeds.
		DR. BORER:  No, no. I'm not asking about surgical bleeds.  I'm not even sure you captured the data I'm asking about, but once somebody went to bypass grafting, I assume they were censored.  Is that correct?
		DR. LUZ:  Let me first show you the data that we have on PCI during infusion.  026, please.  This is just a flowchart to show you how many patients underwent PCI or CABG during study infusion.  If you just focus on the bottom part of the slide, there is a very small number in both groups that actually underwent CABG or PCI during infusion of active study medication.
		This slide summarizes the findings for these patients.  It's a bit crowded and complicated.  I have tried to walk you through that slide.  For both heparin and lepirudin you have three columns.  First, the events in all patients, then events that occurred before the intervention, and events that occurred after intervention.

		The top two rows give you the incidences of CV death MI and CV death MI refractory angina.  To focus on this first, one can see that the total that the overall incidents of both endpoints was higher in the heparin group than in the lepirudin group.
The same observation can be made both for events that occurred before intervention and after the intervention.  Now, if one moves on to discuss safety, the first and most important observation that one can make is that there were no major bleeds in any of these patients.  
		The second point is that there were, in fact, only minor differences in the incidences of minor bleeds.  In fact, the incidences of minor bleeds were higher overall in the heparin group than in the lepirudin group.  Again, this mild trend was observed both for events for and after the intervention.  		It's a small database but it is all we have during infusion.
 		DR. BORER:  What is the intervention?  
		DR. LUZ:  Pardon me?
		DR. BORER:  Can you define intervention for me?  The intervention is the angioplasty or the bypass graft?
		DR. LUZ:  Yes, it's either CABG surgery or PDCA.
		DR. BORER:  Do you have data to answer the question I asked.  That is, to compare the 100 patients that were operated on after lepirudin versus the 100 patients that were operated on after heparin.
		DR. LUZ:  No, I don't have the data.
		DR. BORER:  Okay.  I think that those data should be made available to the FDA because --
		DR. LUZ:  We'll be glad to.
		DR. BORER:  -- it's exactly in that population that we are now seeing important problems with other clot active agents that are being used for acute coronary syndromes.
		DR. PACKER:  Joann.
		DR. LINDENFELD:  The overall rate of the angioplasty or coronary angiography in the first three days of the study during the infusion was what?  Very low.
		DR. LUZ:  It was just the 100 patients so about --
		DR. LINDENFELD:  Again, just as we have concerns about bleeding.  The most common cause of bleeding, of course, is intervention and this had a very low rate of intervention.  I think we just have to be aware that we'll see substantially more bleeding if there is more with more interventions as we would see in the states.
		DR. YUSUF:  (Inaudible.  Off microphone.)
		DR. CALIFF:  I think Joann's point is relevant to U.S. practice that these data are not very relevant because intervention is almost always done the first 48 hours and that makes it difficult.
		DR. LINDENFELD:  And we know that the rate of bleeding if it is higher will be substantially higher with an intervention.
		DR. CALIFF:  Whether that's the appropriate treatment pattern or not is a different issue.
		DR. PACKER:  Ileana.
		DR. PIÑA:  In the FDA review that we've received, there is a listing of adverse events resulting in discontinuation of infusion.  It seems that the hemorrhagic events are twice as many in the lepirudin group.  Are those hemorrhagic -- but you've concluded that there were no excess major bleeds.  Is that part of your going back into the documents and finding that some of the events that were classified as major bleeds were indeed not?
		DR. LUZ:  No.  The determination of whether a bleed was major or not was purely based on the information that was collected on the major bleed form.  We had prespecified criteria that the investigators had to check and depending on whether or not there was a check mark, the bleeding was reported as major and, therefore, further adjudicated or not.
		DR. PIÑA:  To me a hemorrhagic event that leads to the discontinuation of the infusion in my estimate would say that the investigator felt that it was significant enough to stop the infusion.  Then I think that the follow-up to Jeff's point that when you do have bleeding with this agent, what do you give?  Do you give fresh/frozen plasma?  Do you give products?  Do you give whole blood?  What do you give?  You've got time before your half-life has dropped.
		DR. YUSUF:  The most common thing was just to stop the infusion.  That's what people did.  The next most common was give blood.  In no case in the whole study was ultracentrafication needed, although that was one of the things we told people.  Everything was handled by giving blood or stopping the medication.
		DR. LUZ:  In fact, the important point is in the vast majority of cases the discontinuation of infusion per se was sufficient because no transfusion was needed.  The overall frequency of transfusion was in the range of .4 percent.  The early discontinuations were obviously much more frequent.  		In fact, we believe that no difference in the occurrence of life-threatening bleeds might have to do with the early discontinuation that in cases with minor bleeds or ongoing bleeds could be stopped simply by terminating the infusion.
		DR. PIÑA:  And were any of these hemorrhagic bleeds people who received thrombolytic therapy or people that ended up going to interventions?  Do you have that data?
		DR. LUZ:  We have very few patients who concomitantly received thrombolytic agents.  The vast majority of patients who suffered bleed did not receive thrombolytics.
		DR. PACKER:  Rob and then Marv.
		DR. CALIFF:  Two questions.  One is if you just take needing one or more units of blood transfusion in the two groups, what does that look like?  Any transfusion?
		DR. LUZ:  Well, in fact, I think we have only two cases where only one transfusion was given in the vast majority.  This makes sense from a medical point of view there were at least two transfusions.
		DR. CALIFF:  We have those numbers.  There's an excess of transfusion in the --
		DR. LUZ:  Yes.
		DR. CALIFF:  And the second question what would the recommendation be for someone who needs to undergo urgent bypass surgery in this circumstance?
		DR. YUSUF:  (Inaudible.  Off microphone.)
		DR. CALIFF:  So you stop and wait four to five hours to go to surgery.
		DR. YUSUF:  This is a matter of great concern at the beginning, especially at our center.  Our IRB held up our protocol.  Then the chairman called Eric Toppel and I think talked to Chris Granger as well.  Then we came up with the strategy that all you do is wait four to five hours.
		DR. PACKER:  Marv.
		DR. KONSTAM:  You know, looking through the briefing document, I understand there are two sets of data with regard to life-threatening bleeds.  I'll just say my understanding and you tell me if I've got it wrong.  There was an investigator driven definition of life-threatening bleed and then you redefined life-threatening bleed so the data came out two different ways.  But if you stick to the original investigator driven definition of life-threatening bleeds, there were 23 in the lepirudin group and 12 in the heparin group for a p of .089.  Is that right?
		DR. LUZ:  Perhaps we can look at the data and I can try to shed some light on that.  079.  This is a breakdown of bleedings that were reported as life-threatening by the investigator.  I see you just pointed out there were 23 such cases in the lepirudin group and 12 in the heparin group.
		Applying the objective definition of life-threatening, the counts were nine in heparin and seven in lepirudin.
		DR. KONSTAM:  Can I stop you?  When did you come to that definition?  The objective definition.  When did that appear?
		DR. LUZ:  The definition was introduced when the investigator group in Hamilton before unblinding the study --
		DR. KONSTAM:  Before unblinding but they knew there were a lot of bleeds going on.  In other words, yes before unblinding but they had already --
		DR. LUZ:  The overall incidents of major bleeds, as I pointed out, was as low as in the OASIS-1 study so from that point of view there was no reason to be concerned.
		DR. KONSTAM:  Right, but you knew that you had 35 cases that had been designated life-threatening bleeds.  You didn't know that?

		DR. YUSUF:  No.  I'll tell you how this happened, Marvin.  This happened about six months or so before the end of the study when the statistician came to me and I wasn't aware of what was happening, not the event rate or nothing, and said, "Look, we've got several people that are calling events life-threatening bleeds.  They didn't get any IV fluids or blood.  They didn't have an intervention.  They didn't have anything and they didn't have lepirudin, hematoma, nothing.  What should we do?"  
		I said we should have an objective measure not knowing what it will turn out to be.  We had an objective measure put in which is you need to have either hemodynamic instability or the drop in hemoglobin by more than five or needing allotropes or needing a lot of blood transfusions or needing an intervention.  I had absolutely no idea what the overall event rate was on the blinding and I didn't know what had happened later.
		DR. PACKER:  Dr. Farrell who is the FDA medical reviewer for the FDA.
		DR. FARRELL:  I just wanted to focus us.  I was afraid we were going to get off the subject of ischemic strokes.  When I looked at that, there's a definite difference between days eight and 35.  If you are not in favor of lepirudin and if you actually look and subdivide that into weeks, the majority of the strokes occur between days eight and 14.  This may be a drug effect.  It's not true for the heparin group.
		DR. LUZ:  It would be difficult to explain it.  Given that during exactly the same period the incidents of coronary ischemic events were identical in both groups, there was no indication of other ischemic events ongoing.  It seems surprising that the drug should have a specific cerebrovascular effect that causes ischemic strokes.
		DR. KONSTAM:  The designation of ischemic stroke was by the investigator.  Was there always confirmation that there was not a bleed involved?
		DR. LUZ:  Yes.  In 90 percent of all cases the diagnosis was confirmed by CT or MRI and centrally and blinded adjudicated.  In the only six cases where no CT or MRI was done, the diagnosis was uncertain stroke.  That was confirmed by the adjudication committee.  Actually, the adjudication committee confirmed 70 of the 74 reported strokes.
		DR. YUSUF:  (Inaudible.  Off microphone.)
		DR. KONSTAM:  Right, but there were a far greater number of strikes that were designated ischemic than there were designated hemorrhagic bleeds.
		DR. YUSUF:  The deltas.
		DR. KONSTAM:  I understand.
		DR. PACKER:  Okay.  I would like to -- I see there are no other questions.  We have a real need to complete this meeting by 4:00.  I hope we can do that.  I have asked Dr. Hirsh to markedly curtail his presentation.  His original presentation had 26 slides for risk of benefit which, in all honesty, Jack, probably sets an all time record as far as the experience of this committee.  You'll get extra credit for every slide you skip.
		DR. HIRSH:  Okay.  Thanks very much.  Let's go to the next slide.  In this presentation before going to the meat of the presentation, I'll just briefly review the current antithrombotic treatments for acute coronary syndromes.
		Again, I'll just hit the highlights.  There's been this discussion about heparin plus aspirin being more effective than aspirin alone.  I think the evidence is strong that heparin plus aspirin is more effective than aspirin alone.  The debate is just how much more effective is it.
		As you know, in enoxaparin, a low molecular weight heparin, is more effective than heparin and it was approved by this committee based on the triple endpoint of all-cause death, myocardial infarction, and refractory angina.  It was approved on the basis also of the putative placebo.  There are two of the lepirudin studies.  The OASIS-1 and OASIS-2 have been shown to be more effective than heparin on the basis of all-cause death, myocardial infarction, and refractory angina.
		Two other low molecular weight heparins have been studied.  Neither are more effective than heparin and one fragment was approved on the basis of a placebo control study and glycoprotein-IIb for antagonists plus heparin as being compared with placebo and heparin and both of them were approved.
		Now, to go onto the key issues with lepirudin and acute coronary syndromes is that, and we've heard this many times, although the primary endpoint for OASIS-2, which is the double endpoint of seven days, was only borderline significant at p=0.086.  I believe the evidence is persuasive and that hasn't changed.  These slides were made before I heard the presentation and I still believe this, that lepirudin is more effective than heparin and I believe the evidence is compelling that lepirudin is more effective than placebo.
		This is based on the two studies with the triple endpoint at seven days, OASIS-1 and OASIS-2, both significant risk reduction shown here.
		On the pooled analysis of OASIS-1 and 2 for the double endpoint of seven days, which was significant.
		On the analysis that Lloyd Fisher did on the putative placebo where lepirudin was superior to putative placebo and was highly statistically significant.
		Now, Dr. Yusuf has discussed the consistency within class of the OASIS studies.  What I would like to do is discuss the overall consistency and point out that lepirudin -- the data with lepirudin are consistent with similar data from GUSTO-IIb which evaluated desirudin.
		This evaluation is based on OASIS-1 and 2, lepirudin, GUSTO-IIb with desirudin.  The endpoint was all-cause death or myocardial infarction at or close to the end of treatment.  As you'll see on the next slide, the RRR was 26 percent which was highly statistically significant for the combined analysis.
		This shows you the more detailed analysis of those studies.  I would like to point out that OASIS-1 and 2, GUSTO-IIb and, of course, the combined OASIS-1, 2, and GUSTO-IIb were all statistically significant for the endpoint of all-cause death or MI close to or at the end of the treatment period.  We've got to use this to compare this with the other forms of treatment.
		This hasn't been discussed yet so I would like to spend just a little bit of time on this.  This is the discussion of the net clinical benefit with lepirudin.
		The evaluation of net clinical benefit, we used pooled data from OASIS-1 and 2 using an integrated endpoint to find all-cause death, myocardial infarction, disabling stroke, and life-threatening bleed.  This integrated endpoint captures the most serious efficacy and safety outcomes.
		What this shows is that 7.6 of 1,000 patients treated did better with lepirudin than heparin for the quadruple endpoint, all-cause death, myocardial infarction, disabling stroke, and life-threatening bleed.  This was statically significant.
		The integrated endpoint was expanded to add all bleeds and add refractory angina.  That' is shown on the next slide which shows with the expanded integrated endpoint, the benefit in favor of lepirudin was 10.6 patients per 1,000 patients treated.
		Dr. Yusuf discussed the durability of benefit for OASIS-1 and OASIS-2.  This is a discussion, the durability of benefit using the integrated quadruple endpoint.  That is, the net clinical benefit.
		As I mentioned, we used pooled data from OASIS-1 and 2.  What you'll see on the next slide is the results 72 hours, seven days, 35 days, and 180 days.  As you'll see, the effect was durable.
		Dr. Yusuf has shown this slide.  Just concentrate on the numbers in the circle which is the actual risk reduction.  You can see there is neither loss nor gain over the complete period of the study.
		To move to my last point which is a comparison of the relative efficacy and safety of hirudin with two new classes of antithrombotics that have been approved, low molecular weight heparin specifically, enoxaparin, the glycoprotein IIb/IIIa antagonists.
		Now, these comparisons were indirect and they have the limitation of being indirect but I believe they are informative.  Just to point out again that hirudin and low molecular weight heparin were compared with an active-control heparin where the glycoprotein IIb/IIIa antagonists were compared with placebo, both groups receiving heparin.
		The outcome you'll see that is being shown is the all-cause death of myocardial infarction at or close to the end of treatment period.  This is common to all the studies.
		This table shows the relative risk of the p-value for the comparison of all hirudin versus heparin, for enoxaparin versus heparin using the double endpoint at or close to the end of treatment, for all low molecular weight heparin versus heparin, and for GP I put IIb/IIIa antagonists versus placebo.  The effect is significant for these three.  
		The reason it's not for all low molecular weight heparin versus heparin because in two of the studies, as you saw -- well, you saw one of them but in two of the studies, one with FRAX heparin and one with fragment, the low molecular weight heparin was no different than heparin.  Therefore, the relative risk was brought close to the unity when those two were added to the enoxaparin.
		This shows the more detailed analysis.  You've already seen this with the significance for these four including the essence in the TIMI-11B data both of which cross the point of unity.  The Antman meta-analysis at eight days is significant.  And this shows the FRIC and the FRAX.I.S. data.  The point of this slide is that the order of magnitude of benefit seen in the pooled analysis with the hirudin studies is very, very similar to that seen in the Antman meta-analysis.
		This shows the same data for hirudin but now comparing it with the glycoprotein IIb/IIIa.  I would like to concentrate particularly on the comparison of the pooled data with the various studies with hirudin and at 72 hours for the all-cause death myocardial infarction and for the Kong meta-analysis.  Again, the risk reduction is of the same order of magnitude.
		One of the concerns with hirudin has been bleeding.  This is a summary of the major bleeding rates in the OASIS-1 medium dose, OASIS-2, GUSTO-IIb, the low molecular weight heparin studies I showed, and the glycoprotein IIb/IIIa antagonists studies I showed.  
		This, again, just points out that there was a significant increase in bleeding with hirudin in the OASIS-2 and GUSTO-IIb.  This is the GUSTO-IIb, patients only without ST elevation, those not treated with thrombolytic therapy.
		The other point I would like to make is that the order of magnitude of bleeding is similar when one compares the three studies and compares the four studies with low molecular weight heparin.  In three of the studies with glycoprotein IIb/IIIa		 antagonists there was an increase in bleeding with the test drive compared with the control.
		These are my concluding slides.  Although the primary endpoint for OASIS-2, which was cardiovascular death, myocardial infarction at seven days, was only borderline significant.  I still believe that the evidence is persuasive that lepirudin is more effective than heparin and I think it's very persuasive, indeed compelling, that lepirudin is more effective than placebo.
		Within each OASIS study there's a consistency of benefit across different endpoints and the different time points.  The effects are consistent across both OASIS studies and data with lepirudin are consistent single data from the GUSTO-2b study with desirudin.  There's enormous consistency.  This provides a totality of data.
		The risk reduction with lepirudin is of the same order of magnitude of enoxaparin.  It is also the same order of magnitude as the GP IIb/IIIa antagonists.  
		As you've heard, there is an absolute increase in major bleeding with lepirudin which is small and similar to that seen with GP IIb/IIIa antagonists.  From the net clinical benefit, the integrated clinical endpoint, the increase in bleeding is more than offset by benefit from serious efficacy outcomes.
		So at the end of the day I still believe that lepirudin represents an important addition to currently available antithrombotic agents for treatment of patients with acute coronary syndromes.  Thank you.
		DR. PACKER:  Thank you very much, Dr. Hirsh.  Questions?  If not, the committee will proceed directly to the questions that are before it.  I'm not going to read the introduction but I will go through questions 1 through 6.  We have absentee votes from four members of the committee and we'll begin with our primary reviewer.  
		The first question asks whether refractory angina is an acceptable component as it is defined and assessed in the OASIS-2 trial.  We'll begin the voting with Dr. Borer.
		DR. BORER:  Yes, I believe it is.  First of all, I think that in the OASIS-2 definition intervention was a part of it so I think the question may be slightly incorrectly worded but it doesn't matter.  Whether it did or didn't, most of the patients who had an angina endpoint had an intervention and I just don't believe this is an issue.  I think that the definition of angina is acceptable and that it is an acceptable component of the endpoint.
		DR. PACKER:  Does anyone -- we need to go through this so we'll just start from Marv.  Do you want to say yes or no?

		DR. KONSTAM:  Yes.
		DR. FLEMING:  Yes.
		DR. LINDENFELD:  Yes.
		DR. CALIFF:  Yes, but a comment that this endpoint needs a higher level of statistical certainty to be acceptable because it's less compelling than irreversible endpoints.
		DR. DIMARCO:  Yes.
		DR. PACKER:  And yes.  The vote of Dr. Graboys is no, Dr. Grines yes, Dr. Piña no, and Dr. Armstrong yes.  The total vote is nine yes and two no. 		Question No. 2.  Has adequate evidence been presented to demonstrate that the heparin regimens used in the OASIS trials were effective in the study population (patients with unstable angina or acute MI without ST segment elevation)?  We have discussed this at great length.  We need to vote.  Dr. Borer.
		DR. BORER:  Okay.  Intuitively I think heparin is likely to be better than placebo.  I fully support the use of historical data for creation of comparisons to evaluate the efficacy of new therapies when you can't do placebo control trials anymore.  		However, I am very concerned that the evidentiary base for the putative placebo here is unacceptably weak and I have difficulty saying that because it's in contra distinction to what Dr. Hirsh said and there's no one in the world who is more highly respected in this area than he is.  Nonetheless, I would have to vote no.  I don't think adequate evidence has been presented to demonstrate that the heparin regimens were effective.
		DR. PACKER:  Okay.  And we'll begin with John on this side.  We'll just go through the vote.
		DR. DIMARCO:  I'll agree with Jeff that the evidence isn't great for heparin but I think it's going to be really impossible to do a heparin/placebo trial so I think we're stuck with what we have and what we have is clinical practice so I will say this is the standard regimen, this is standard use clinically, and there is some evidence in support of it so I would say yes.
		DR. PACKER:  Okay.  We'll leave it at that.  Rob.

		DR. CALIFF:  I say yes also.  The question to me is not whether heparin is effective.  It's how effective is it.  I think it's hard to tell how effective it is but to me all the trials go the same way.
		DR. PACKER:  Joann.
		DR. LINDENFELD:  I would say no.  I'm just not sure I could say specifically that heparin is effective on the basis of the data we've seen.
		DR. PACKER:  Tom.
		DR. FLEMING:  Milt, I'm adjusting to the world of this advisory committee.  On other advisory committees I don't get pinned to yes and no and as a statistician it's awfully hard to make this dichotomous.  I will give you an answer but let me precede it by saying that the OASIS study was a wonderfully conducted study providing a large amount of data giving us considerable insights about the relative efficacy to heparin.  The cliche is you can't make silk out of a -- I would have to say the analysis by Dr. Fisher was on target for what could be done with the data that are available.
		DR. PACKER:  We shouldn't confuse issues here.  This is not a question about the agent which is the target of this NDA.  This is a question about heparin.  I just want to clarify that.
		DR. FLEMING:  I understand.  I understand.  To finish the thought, the evidence as it has been provided to us about heparin is inadequate.  Not because of the statistical methodology but because of the available data.  In essence my answer is no, the data do not adequately demonstrate that the heparin regimen was effective in essence, in my view.  		Historical data and clinical insight would have to establish that the effect is on the order of 10 to 12 percent at 35 days and it would have to be based on that experience.  I can only respond to the data presented to us so my answer would be no.
		DR. PACKER:  Okay.  Marv.
		DR. KONSTAM:  I'm going to vote yes but I'm going to also say that I'm lowering my standards to do so and it's in the context of the vote of public opinion that the medical community feels overwhelmingly that heparin is an effective agent in this setting and that handcuffs the trials that can be done.  
		Of the data that were provided, I would say that the FRIC and FRISC combination are probably more convincing than the Oler meta-analysis.  I will say under other circumstances that level of data would not be sufficient for me to say this but in the present context I'm going to vote yes.
		DR. PACKER:  I'm going to vote no.  I just want to emphasis that I do believe that heparin works but the question does ask has adequate evidence been presented which leads me to vote no.  I'm not certain that my vote is incompatible with those who have voted yes.  
		The votes of Dr. Graboys yes, Grines yes, Piña yes, Armstrong yes.  The final vote is seven yes, four no.
		Third question.  Do the data provide adequate evidence of the effectiveness of Refludan for its proposed indication?  We'll begin again with Dr. Borer.
		DR. BORER:  Again, intuitively as I said about heparin and placebo based on the data we've seen, intuitively I think that lepirudin is more effective than heparin.  I think the active comparison is highly suggestive but because of my concern about the putative placebo, I think that by itself it's not really sufficient to support a reasonable conclusion.  		It doesn't say it's not better but a reasonable conclusion.  It's a single trial.  It's smaller therapeutic effect than was expected.  There are some safety concerns that haven't been fully evaluated.  I am concerned that OASIS didn't support its primary hypothesis but this by itself really wouldn't necessarily cause me to withhold an approval recommendation if all the other data were compelling.  		I don't think all the other data are sufficiently compelling and, therefore, I don't think it's appropriate to set the precedent that approval should be provided based on a single sort of marginally significant trial of a new drug versus an active comparator when the active comparator hasn't been shown rigorously to be better than placebo, or at least acceptably better than placebo.  I don't think that we've reached the standard that I would set for this particular drug from this particular trial.
		DR. PACKER:  Okay.  Dr. Borer's vote is no.  Which side did we start on the last time?  I'm sorry.  John.
		DR. DIMARCO:  As I read the new indication, there's nothing in there that states that it is superior to heparin so I would vote yes.
		DR. PACKER:  Rob.
		DR. CALIFF:  I'm going to take 20 seconds on a soapbox or maybe a little longer.  I've got all the pluses and minuses here.  This is a very difficult one for me.  On the plus side we've got two studies going in the right direction.  You only have to believe that heparin is a bit better than placebo to buy the putative placebo argument.  I believe it is.
		The complete systematic overview of all the hirudins that Dr. Hirsh sneaked by in the last few minutes is pretty compelling, I think.  We are dealing with a leading cause of death and disability.  I'm worried that the standard for this in heart failure are getting so high that it's going to discourage drug development in these areas.  
		Looking at what it takes to get drugs through other committees and the FDA, this is an incredibly high standard.  We need better agents for this condition particularly with the combinations that need to be given and this drug is already approved for heparin-induced thrombocytopenia.  		It would be a funny situation to say that a drug should be used in place of heparin when you produce thrombocytopenia but there's no reason to use the drug which is kind of the conclusion that we'll be coming to.  Finally --
		DR. PACKER:  We see that.
		DR. CALIFF:  Well, I mean, it's kind of dumb.  Then finally --
		DR. PACKER:  We see lots of dumb things.
		DR. CALIFF:  So then finally there would be no surprises, I think.  There is a lot of data and nothing surprising except for the ischemic stroke issue has really come out of this whole discussion.
		On the minus side, the primary study, the heparin overview is pretty weak.  We would all agree and wish it was better.  I'm particularly concerned about publication bias.  There is an excess of bleeding.  The treatment is dependent on renal function and we've learned a lot in the last year about the difficulty U.S. physicians have in understanding creatinine clearance and the problems that might arise.  
		The study is not very relevant to the U.S. practice.  There's no African Americans and there's almost no coronary intervention.  This is really around the border for me but I think I would have to vote yes on this and it's pretty subjective.  I could go either way but I think I have to vote yes.
		DR. PACKER:  Joann.
		DR. LINDENFELD:  Rob said it well.  For all those same reasons I'm right on the fence, too, but I think I would vote yes.
		DR. PACKER:  Tom.
		DR. FLEMING:  For the information that I was giving in my previous answer, the effect with the OASIS study is establishing about a 12 percent reduction in death MI at 35 days.  In fact, it had achieved what it had been powered to achieve.  The study itself could well have carried the day.  
		If, in fact, we could be confident, highly confident that heparin itself provides about a 12 percent reduction in death MI at 35 days, then I would believe this is convincing data.  The evidence has not been presented to be that convincing.
		Rob points out, of course, the high number of patients that we would need to see in order to provide clear evidence, for example, at a seven or 35-day time point.  Of course, the reality for that is this is a clinically very important issue but it's also one where we have to recognize we are only preventing a small fraction of the total events and that's the reason that it's taking such a large study to be able to sort out whether you're having a small effect or no effect.  
		Because, as I indicated in my answer to No. 2, the data here don't provide clear evidence that establishes that heparin itself is providing roughly a 12 percent reduction in death MI at 35 days, my vote is no.  I believe that evidence would have to be in hand to make it yes.
		DR. KONSTAM:  As Rob indicated, we have this tough situation where essentially the entire medical community practices in a way that has not been acknowledged based on hard data, I guess, by the FDA that it is effective.  Nevertheless, that is the situation and we have to make a decision whether that situation is going to handcuff any additional progress or we can figure out a way to make things move on.
		When I look at this DNA, the heart of the DNA is the OASIS-2 trial.  Looking at the primary endpoint as well as all other endpoints and all time points, I'm most impressed by the right sided confidence interval which is right about one in a 10,000 patient trial.  I feel this trial is fairly convincing for at least equivalence to heparin.  
		Then we have to come back and say do we believe heparin works or not.  As I indicated in my answer to the previous question, the medical community is voting with its feet overwhelmingly that it works and I believe the data that was presented here today at least supports that and so, therefore, I'll vote yes.
		DR. PACKER:  I think that Rob summarized it well.  It's really a matter of judgment as to how you weigh all the factors.  I think that the way that I would weigh the factors would probably go more towards Tom concerns and I would vote no.
		The votes for Dr. Graboys no, Grines no, Piña no, Armstrong no.  The votes are seven no, four yes.
		No. 4, do you have safety concerns regarding Refludan for this indication, bleeding complications, etc.  Jeff?
		DR. BORER:  Well, I think there are issues that need to be better defined.  Personally, as I've made clear during the discussion today, I think we need to know what complications we can expect, or rather how to handle the follow-on therapies that are likely to be used in practice, particularly bypass grafting, so I think those data need to be put together.
		I'm concerned about the excess of strokes in the eight to 35-day period, particularly eight to 14 days.  I can't explain it.  It doesn't really seem to fit into my understanding the pathophysiology but that doesn't mean very much because often we don't understand the way drugs work.  I would like to see that better defined so, yes, I think there are some safety concerns here that need to be explored further.
		DR. PACKER:  So that's a yes.  We'll begin with Marv.
		DR. KONSTAM:  I'm concerned about the bleeds.  I think at the dose used we have bleeds clearly in excess of what we see with heparin and I'm concerned that the bleeds that were considered by the investigators to be life-threatening bleeds seem to be significantly more frequent than with heparin so I am concerned about those things.
		The ischemic stroke issue also is concerning.  I'm confused by it because I don't have any explanation for it but I think that is something else to be a little concerned about.
		DR. PACKER:  Tom.
		DR. FLEMING:  Yes.  Just a quick comment.  Marv has indicated similar perspectives.  The major bleeds and the ischemic strokes are the issues that strike me as of greatest concern and this is somewhat related to the next question.  There really are two relative comparisons for safety as well.  If we're looking at just deciding what the relative safety is to the active comparator, then it's the safety comparison that we see in the clinical trial.
		On the other hand, if we're thinking efficacy is against the putative placebo, then we also have to think of the safety experience against what the safety experience would be of the putative placebo.  We have to add in those additional safety experiences that we think are due to the active comparator.
		DR. PACKER:  Okay.  Rob.  Oh, I'm sorry.
		DR. LINDENFELD:  I have additional concerns, particularly when there is a much higher rate of intervention as we have in the states.
		DR. PACKER:  Rob.
		DR. CALIFF:  I would vote no on this but for two reasons.  One, there's a whole bunch of other hirudin data from angioplasty trials and others that I know about that wasn't presented here.  Secondly, I think you know what you see is what you're going to get which is a modest excess of bleeding in 20,000 or so patients.  That's a much better database than most other treatments we have but the whole committee hasn't seen all the data.
		DR. PACKER:  John.
		DR. DIMARCO:  Other than the first word, I would say yes, I have safety concerns for exactly the same reasons that Rob just mentioned he didn't.  I think there's probably going to be a price to pay with a drug like this and bleeding is going to be the side effect and people are going to have to be concerned about it.
		DR. PACKER:  My vote is yes.  All absentee votes were yes so the vote on this is 10 to one.  Fifth question.  Given the data from the OASIS trials, do you believe the benefits of Refludan exceed its risks for the sponsor's proposed indication?  Why don't we pause there and, Jeff, why don't you lead off the vote.
		DR. BORER:  Well, I've already indicated that I don't think the benefit has been compellingly demonstrated and, therefore, obviously, I can't say that it exceeds the risk.  Do you want --
		DR. PACKER:  That's sufficient.  That's sufficient.  Okay.  And, Marv, why don't we start with you.
		DR. KONSTAM:  Yes, and in the dose that was used in OASIS-2.
		DR. PACKER:  Why don't we go yes and no because it will just make life easier.  Marv is yes.  		DR. LINDENFELD:  Yes.
		DR. PACKER:  All right.  Tom.
		DR. FLEMING:  Do I believe benefits exceeded the risks?  No, I don't believe it's been proven adequately that benefits exceed the risks and, again, a reminder that if we are thinking of that against the putative placebo, we have to be thinking of all of the risks that are associated with the intervention and not just the increase relative to the active comparator.
		DR. PACKER:  Joann?
		DR. LINDENFELD:  Yes.
		DR. PACKER:  The answer for Joann is yes.  Let me just make sure.
		DR. CALIFF:  Milton, I vote yes.  I've got to catch a plane.
		DR. PACKER:  John.
		DR. DIMARCO:  I'll vote yes.
		DR. PACKER:  My vote is no.  Graboys' vote was no.  Grines vote no.  Piña's vote no.  Armstrong's vote no.  It is seven to four no.  Six is not relevant and the remainder of five is what further studies would one advise.  I'm not certain how one would address that question.  I think that is really for the sponsor to propose based on all discussions and concerns that have been expressed.
		Any other comments?
		DR. BORER:  I would just like to make one point here.  I don't believe and some other members of the committee suggested they didn't believe that the benefits of heparin were clearly demonstrated.  I would certainly believe that there is no evidence to suggest that heparin is worse than placebo.  
		If somebody wanted to do the kind of comparison that was just done, and this is a difficult study to do, if somebody wanted to replicate these data, I think that would be a perfectly reasonable thing to want to do.
		DR. PACKER:  There being no further comments, we are adjourned.
		(Whereupon, at 4:09 p.m. the meeting was adjourned.)