FOOD AND DRUG ADMINISTRATION
        
          CENTER FOR DRUG EVALUATION AND RESEARCH
        
        
        
        
        
                     EIGHTIETH MEETING
        
                           OF THE
        
        CARDIOVASCULAR AND RENAL DRUGS ADVISORY COMMITTEE
        
        
        
        
        
        
        
        
        
        
                         8:30 a.m.
                Thursday, February 27, 1997
        
        
        
        
        
        
        
        
        
        
        
        
                   Jack Masur Auditorium
                Building 10, Clinical Center
               National Institutes of Health
                    9000 Rockville Pike
                             Bethesda, Maryland                        APPEARANCES
        
        COMMITTEE MEMBERS:
        
        BARRY MASSIE, M.D., Chairman  (present morning session)
        Director, Coronary Care Unit
        Department of Medicine
        Veterans Administration Hospital
        4150 Clement Street
        San Francisco, California  94121
        
        JOAN C. STANDAERT, Executive Secretary
        Center for Drug Evaluation and Research
        Food and Drug Administration
        234 Summit Street, Room 117
        Toledo, Ohio  43604
        
        ROBERT CALIFF, M.D. (present afternoon session)
        Professor of Medicine
        Director, Duke Clinical Research Center
        Duke University Medical Center
        2024 West Main Street, Box 31123
        Durham, North Carolina  27707
        
        JOHN DiMARCO, M.D.
        Professor of Medicine
        Cardiovascular Division
        University of Virginia Hospital, Box 158
        Hospital Drive, 5th Floor
        Private Clinic, Room 3608
        Charlottesville, Virginia  22908
        
        CINDY GRINES, M.D.
        Director, Cardiac Catheterization
        Division of Cardiovascular Disease
        William Beaumont Hospital
        3601 West Thirteenth Mile Road
        Royal Oak, Michigan  48073-6769
        
        MARVIN KONSTAM, M.D.
        Professor of Medicine
        New England Medical Center
        750 Washington Street, Box 108
                Boston, Massachusetts  02111                        APPEARANCES
        
        COMMITTEE MEMBERS:  (Continued)
        
        JoANN LINDENFELD, M.D. (present morning session)
        Professor of Medicine
        Division of Cardiology
        University of Colorado Health Science Center
        4200 East Ninth Avenue, B-130
        Denver, Colorado  80262
        
        LEMUEL MOYE, M.D., PH.D.
        Associate Professor of Biometry
        University of Texas Health Science Center
          at Houston
        Coordinating Center for Clinical Trials
        1200 Herman Pressler Street, Suite 801
        Houston, Texas  77030
        
        CYNTHIA RAEHL, PHARM.D.
        Consumer Representative
        Chair, Pharmacy Department
        School of Pharmacy
        Texas Technical University
        Health Science Center
        1300 South Coulter Drive
        Amarillo, Texas  79106-9711
        
        DAN RODEN, M.D.C.M.
        Vanderbilt University
        Division of Clinical Pharmacology
        532C Medical Research Building-1
        23rd and Pierce Avenue
        Nashville, Tennessee  37232-6602
        
        UDHO THADANI, FRCP (present morning session)
        Professor of Medicine
        Division of Cardiology
        Oklahoma University Health Sciences Center
        920 S.L. Young Boulevard, 5-SP-300
        Oklahoma City, Oklahoma  73104
        
        MICHAEL WEBER, M.D.
        Chairman, Department of Medicine
        Brookville University Hospital Medical Center
        1 Brookville Plaza
                Brooklyn, New York  11212                        APPEARANCES
        
        COMMITTEE CONSULTANTS:
        
        JEFFREY BORER, M.D.
        ROBERT CODY, M.D. (present morning session)
        RALPH D'AGOSTINO, PH.D.
        
        
        FOOD AND DRUG ADMINISTRATION STAFF:  
        
        BOB FENICHEL, M.D.
        RAYMOND LIPICKY, M.D.
        NORMAN STOCKBRIDGE, M.D.
        ROBERT TEMPLE, M.D.
        
        
        MEDCO REPRESENTATIVES:
        
        JAY COHN, M.D.
        LLOYD FISHER, PH.D.
        CESARE ORLANDI, M.D.
        JOSEPH QUINN, M.S.P.H.
        
        
        SMITHKLINE BEECHAM REPRESENTATIVES:
        
        WILSON COLUCCI, M.D.
        LLOYD FISHER, PH.D.
        MILTON PACKER, M.D.
        ROBERT L. POWELL, PH.D.
        NEIL SHUSTERMAN, M.D.
                JIM TIEDE, PH.D.                      C O N T E N T S
                      MORNING SESSION
        
                     NDA 20-727, BIDIL
         (hydralazine HCl and isosorbide dinitrate)
        to be indicated for congestive heart failure
        
        
        AGENDA ITEM                                    PAGE
        
        OPEN PUBLIC HEARING                               7
        
        
        MEDCO RESEARCH, INC. PRESENTATION:
          Introduction 
            by Dr. Cesare Orlandi                        11
        
          Historical Overview, Clinical Efficacy
            by Dr. Jay Cohn                              12
        
          Statistical Overview 
            by Dr. Joseph Quinn                          32
        
          Summary/Conclusions 
            by Dr. Jay Cohn                              44
        
        
        COMMITTEE REVIEW AND DISCUSSION                 114
                                      C O N T E N T S
                     AFTERNOON SESSION
        
            NDA 20-297 s-001, COREG (carvedilol)
        to be indicated for congestive heart failure
        
        
        AGENDA ITEM                                    PAGE
        
        SMITHKLINE BEECHAM PRESENTATION
        
          Introduction - by Dr. Robert Powell           205
        
          Clinical Program - by Dr. Neil Shusterman     213
        
        
                COMMITTEE REVIEW AND DISCUSSION                 303                   P R O C E E D I N G S
                                                (8:30 a.m.)
                 DR. MASSIE:  I want to welcome everybody to the
        80th meeting of the Cardio-Renal Advisory Panel which we're
        going to have today.  
                 Before getting started, let me briefly just
        introduce the members of the committee who are sitting from
        my left to my right:  Dr. Dan Roden, Dr. Marvin Konstam,
        Dr. Cynthia Raehl, Dr. Michael Weber, Dr. Lemuel Moye, Dr.
        JoAnn Lindenfeld, our Secretary, Joan Standaert, Dr.
        DiMarco, Dr. Rob Califf, Dr. Udho Thadani, and not yet but
        to come later, Dr. Cynthia Grines.  Dr. Lipicky
        representing the Division of Cardio-Renal Drugs is on the
        far left, and I guess Dr. Temple will be joining us.
                 In addition, we have several outside
        consultants for today's meeting.  Dr. Ralph D'Agostino, who
        will be a voting member as a special government employee,
        as will Dr. Jeffrey Borer, and Dr. Robert Cody is our
        special consultant, but unfortunately not able to vote.
                 The first order of business is that we are open
        for public comment.  If anybody has any comments, we'd be
        happy to entertain them at this time.
                 In the absence of public comment, we can
        proceed with our business.  Joan Standaert is going to
        discuss the waivers and potential conflicts of interest of
        the committee members.
                 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 for the meeting
        and all financial interests reported by the committee
        participants, it has been determined that all interests in
        firms regulated by the Center for Drug Evaluation and
        Research present no potential for an appearance of a
        conflict of interest at this meeting, with the following
        exceptions.
                 In accordance with 18 U.S.C. 208(b), full
        waivers have been granted to Drs. Barry Massie, Lemuel
        Moye, and Dr. Robert Califf, which permit them to
        participate in all official matters concerning Posicor.  In
        addition, Dr. Dan Roden and Dr. Udho Thadani are excluded
        from participating in all official matters concerning
        Posicor.
                 Further, in accordance with 18 U.S.C.
        208(b)(3), a limited waiver has been granted to Dr. Udho
        Thadani.
                 I'm sorry.  I'm reading the wrong announcement. 
        Well, I'll start over again.   Sorry, excuse me.  We'll do
        that again tomorrow.
                 This is the announcement for February 27th,
        1997.  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 for the meeting
        and all financial interests reported by the committee
        participants, it has been determined that all interests in
        firms regulated by the Center for Drug Evaluation and
        Research present no potential for an appearance of a
        conflict of interest at this meeting, with the following
        exceptions.
                 In accordance with 18 U.S.C. 208(b)(3) full
        waivers have been granted to Drs. JoAnn Lindenfeld, Lemuel
        Moye, Marvin Konstam, and Dr. Dan Roden, which permit them
        to participate in all official matters concerning BiDil. 
        In addition, Dr. Robert Califf is excluded from
        participating in all official matters concerning BiDil. 
        Further, in accordance with 18 U.S.C. 208(b)(3), a waiver
        has been granted to Dr. Marvin Konstam, which permits him
        to participate in all official matters concerning Coreg.
                 However, Drs. Barry Massie, JoAnn Lindenfeld,
        and Dr. Udho Thadani are excluded from participating in all
        official matters regarding Coreg.  
                 Copies of the waiver statements may be obtained
        by submitting a written request to the agency's Freedom of
        Information Office, Room 12A-30 of the Parklawn Building.  
                 We would also like to disclose for the record
        that Dr. Robert Califf and his employer, the Duke
        University Medical Center, have interests which do not
        constitute a 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 that notwithstanding
        these involvements, that the interest of the government in
        Dr. Califf's participation outweighs the concern that the
        integrity of the agency's programs and operations may be
        questioned.  Therefore, Dr. Califf may participate in all
        official matters concerning Coreg.
                 With respect to FDA's invited guest expert, Dr.
        Robert J. Cody has reported interests which we believe
        should be made public to allow the participants to
        objectively evaluate his comments.  Dr. Cody would like to
        disclose that he has conducted clinical trials and
        consulted for SmithKline Beecham, Merck, and Zeneca.  He
        has also given presentations which were sponsored by
        SmithKline Beecham, and Merck.
                 In the event that the discussions involve any
        other products or firms not already on the agenda for which
        an FDA participant 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 statement for February 27th,
        1997.
                 DR. MASSIE:  Thank you very much, Joan.  
                 Well, as is probably apparent to all the
        members of this audience, as well as all the committee
        members, we have a very full agenda today and I'm going to
        do my best to keep the first half on time.  In the interest
        of trying to proceed smoothly, I'm going to ask the
        committee members to try not to interrupt the sponsor's
        presentation midstream because we will allow a block of
        time for questions thereafter and I think that will allow
        the information to flow more smoothly.
                 So, I guess we are ready for the presentation
        for BiDil, NDA 20-727.
                 DR. ORLANDI:  Dr. Massie, members of the
        committee, Dr. Lipicky, ladies and gentlemen, good morning.
                 We are here today to present you BiDil for the
        treatment of congestive heart failure.  BiDil is a
        formulation of two drugs you are very familiar with,
        hydralazine and isosorbide dinitrate.  
                 Our application is based on two landmark
        clinical trials conducted in the 80s by the Veterans
        Administration, the V-HeFT I and V-HeFT II studies.  Based
        on the results of these studies, we propose that BiDil is
        useful in the treatment of congestive heart failure as an
        adjunct to digitalis and diuretics.  It is our opinion also
        that it's most appropriate the use of this formulation in
        patients that are not taking ACE inhibitors, which have
        become also part of standard therapy.
                 Dr. Jay Cohn, who led the V-HeFT trials effort,
        will provide a historical overview of the trials.  Mr. Joe
        Quinn will then address specific statistical issues that
        have been raised by the agency.  And Dr. Cohn will also
        conclude our presentation with a brief summary of the
        findings.
                 I just wanted to mention briefly that we have a
        number of consultants in the audience to address any
        specific question that the committee may have.  This list
        includes Dr. Lloyd Fisher, who conducted a re-analysis of
        the V-HeFT trials, Dr. Uri Elkayam, Dr. Krik Adams, Dr. Ho-Leung Fung, and Dr. Alan Forrest.
                 Dr. Cohn?
                 DR. COHN:  Thank you very much, Cesare, and I'd
        like to express my appreciation to the FDA and to the
        committee for giving me the opportunity to review with you
        the trials that we initiated really almost 20 years ago
        with the planning of the first V-HeFT trial, the
        vasodilator heart failure trials, which have continued to
        date, and the results of these first two trials will be the
        basis for our discussion this morning.
                 What we would like to propose to you at the end
        of this presentation is that there is a strong basis for
        approval of BiDil for heart failure and we would propose
        that this be based on a survival benefit for BiDil as
        compared to placebo, on the basis of a strong trend from
        proved exercise tolerance versus both placebo and versus
        Enalapril in these two trials, on the basis of a sustained
        increase in ejection fraction that we believe not only
        confirms the mechanism of action of this drug combination
        but also confirms that there is a long-term effect of this
        drug combination.
                 This combination of therapy has a well
        established rationale and an even better rationale today
        than at the time these studies were initiated, and we'll go
        into that in the course of this presentation.
                 The safety of this drug combination of these
        two long-used agents is well established.  
                 This combination is already widely recommended
        as a treatment option in essentially all of the treatment
        guidelines that have been published in the last few years.
                 And the approval of this combination is
        required to provide prescribing information to physicians
        who have been told to use this drug combination.
                 Now then, hydralazine and isosorbide dinitrate
        were first used in combination.  We did this, and Joe
        Franciosa, who worked with me at that time, is in the
        audience here today.  We did this on the basis of the
        potency of this combination as a vasodilator, and the
        dramatic acute hemodynamic effect that this drug
        combination produced.
                 At that time we predicted that this favorable
        hemodynamic effect might be translated into a long-term
        benefit but there were no long-term data available in order
        to determine that.  V-HeFT, then, was organized as a
        landmark heart failure study, the first mortality trial
        undertaken in heart failure, with a goal to assess long-term efficacy of this vasodilator therapy added to
        conventional therapy, which at that time was digitalis and
        diuretics.  ACE inhibitors had not been developed at that
        time.
                 And it was possible, of course, at that time to
        include a placebo group because there was no other
        effective therapy, and this provided the first and, I must
        say, the only data that will exist either now or in the
        future of digitalis-diuretic therapy with placebo added in
        long-term therapy of heart failure.
                 We would suggest that the impact of the
        findings of V-HeFT are that there is now demonstrated
        efficacy of chronic therapy, and this was indeed the first
        therapy which was demonstrated to be effective, and it has
        provided a new treatment option for the management of the
        patient with heart failure, which has already been accepted
        by most guideline committees.
                 Well, V-HeFT I was a trial assessing
        vasodilator therapy in long-term therapy compared to
        placebo, added to, as I pointed out, digoxin and diuretic
        therapy for patients with heart failure.  The two
        vasodilator regimens that were employed in this study were
        the hydralazine isosorbide dinitrate combination, and an
        alternate vasodilator, Prazosin, which had a rather similar
        hemodynamic effect in this patient population when given
        acutely.
                 The comparison of the survival times between
        the placebo arm and the vasodilator arms was proposed to
        use a one-sided hypothesis because there was no reason at
        that point to consider any adverse effect of this therapy. 
        The question was, is the therapy effective.  So, it was a
        one-sided hypothesis, and therefore one-sided tests were
        proposed.
                 V-HeFT II was initiated after the completion of
        V-HeFT I, and it was undertaken to determine whether the
        effective arm in V-HeFT I, that is the hydralazine-isosorbide dinitrate arm, had an effect comparable or
        different from that of Enalapril, which at that point in
        time had already been evaluated for short-term therapy of
        heart failure and it appeared to be effective.  These drugs
        then were added to pre-existing conventional therapy of
        digoxin and diuretic.
                 No placebo arm was included in V-HeFT II
        because it was felt by the planning committee that it was
        unethical after the results of V-HeFT I to have a placebo-treated group for long-term therapy.  And since it was not
        known which of the two treatment arms would be more
        beneficial, it was a two-sided hypothesis and two-sided
        tests that were employed.
                 Now, these trials that I'm going to tell you
        about were both randomized, double-blinded.  One was
        placebo-controlled, the other had a positive control.  All
        patients were followed for at least 6 months after
        randomization into the trial, and the survival status was
        confirmed in all patients at the planned date of completion
        of the trial.  Both of these trials were planned to be
        completed at a specific date, and that date was indeed
        utilized in termination of the trial.
                 The inclusion criteria were all males.  The
        studies were all performed in Veterans Affairs hospitals. 
        They were males between the ages of 18 and 75.  They had a
        history of heart failure, with limitation of exercise
        tolerance for at least 3 months prior to screening.  They
        all remained symptomatic, despite the use of digoxin and
        diuretics, and they had objective measurements that made
        them eligible.  That is, there was cardiac dysfunction, as
        defined by either an enlarged heart on chest x-ray, greater
        than .55 cardiothoracic ratio, or a radionuclide ejection
        fraction of less than 45 percent, or a dilated left
        ventricle on echocardiography with a left ventricular
        internal dimension and diastole of greater than 2.7
        centimeters per meter squared.  These criteria were used in
        both trials.
                 In addition, the patients were all subjected to
        a bicycle ergometer exercise test with measurement of gas
        exchange.  And they had to have a reduced peak oxygen
        consumption less than 25 ml per kilogram per minute to be
        eligible for the trial.
                 The major endpoint in both trials was survival
        time, and two related endpoints were utilized.  That is,
        the overall survival, and of course the 2-year survival. 
        Of course, the reason for doing that is that if one follows
        patients long enough, everyone will die and it was thought
        that perhaps a 2-year endpoint might be a more sensitive
        marker for a favorable effect of the therapy.  So, these
        were both proposed as analytical endpoints.
                 Now, the survival time was proposed to be
        carried out by the log-rank test, with the addition of a
        Cox proportional hazards model, using baseline patient
        characteristics as modifiers for the Cox model.
                 I will, in addition, talk to you abut two major
        endpoints of the trial, secondary endpoints, at least. 
        That is, changes in left ventricular ejection fraction and
        changes in peak oxygen consumption, both of which are the
        major determinants of survival in this population.  These
        two endpoints were selected by the FDA with its consultant
        Milton Packer, and Milton is in the audience if there are
        any questions about his selection of these two as two of
        the criteria on which to adjust the mortality with the Cox
        analysis.
                 These, we all agree, are major endpoints in the
        management of heart failure, so that these two I will talk
        to you about in some detail.  These were assessed by
        repeated measures analysis, and the t-test of change from
        baseline by individual visits was utilized for statistical
        analysis.
                 Well, these are the patient characteristics in
        the two trials.  I think you can see that the
        characteristics in the two patient populations are quite
        similar.  That is, the patients were somewhere between 58
        and 60 years old, a little older in V-HeFT II.  The study
        was obviously performed later.  The ejection fraction
        ranged around 28 to 29 or 30 percent in both trials.  The
        cardiothoracic ratio exhibited an enlarged heart in both
        studies.  The peak oxygen consumption averaged around 15 or
        14 ml per kilogram per minute, and patients all had heart
        failure for at least 2 or 3 years.
                 The majority of the patients were Caucasian. 
        That is, about 70 percent of them in both trials, but there
        was a fairly sizeable number of African-Americans in the
        trial.  We won't go into that, but we have much data
        comparing the Caucasian and African-American responses.  
                 This is the duration of heart failure, which
        predominantly was between 6 and 48 months.  About 55
        percent of the patients had coronary disease as the
        etiology of their heart failure, and about 45 percent had
        what was thought to be non-ischemic cardiomyopathy.
                 Now, this was the major endpoint of the trial,
        which was to monitor mortality, and I plot here the
        differences between the placebo and the hydralazine-isosorbide dinitrate groups during the 4-plus years in
        which the patients were followed.  You can see that at the
        initiation there were 273 placebo patients and 186
        hydralazine-isosorbide dinitrate patients.  That was a
        planned preference for placebo entrance because we had a
        third treatment arm, which was Prazosin, which I don't have
        plotted here.  I'll show you the survival curves, including
        Prazosin, in a moment.  But this was an attempt to have a
        larger placebo group so that we could have more confidence
        in the placebo arm.  
                 You can see at the end of 1 year, there had
        been a 19.5 percent mortality in the placebo arm, and a
        12.1 percent mortality with H/ISDN, and that was a 38
        percent mortality reduction.
                 At the end of 2 years, the differences were 34
        and 25.6 percent, or a 25 percent reduction.  At 3 years
        the reduction was at 23 percent, and by 4 years it was a
        little under 10 percent.  By 5 years, of course, the
        numbers became very small.  So, after 3 years we really
        have very little power and obviously an instability of the
        survival curves at that point in time.
                 This indeed is a plot of the three survival
        curves in V-HeFT I.  H/ISDN in yellow at the top showing
        that there is a clear reduced mortality or improved
        survival in this treatment compared to the placebo group in
        blue.  The Prazosin group in red, superimposes on the
        placebo group until this very terminal end, where there's
        great instability in the numbers.
                 I think this was the first evidence that a
        potent vasodilator, which Prazosin is, is not necessarily
        effective in heart failure, so the original concept that
        the two vasodilator arms would behave similarly was
        contradicted by this study.  We now know that the efficacy
        of the vasodilator chronically is not necessarily related
        to its hemodynamic effect.
                 This is just a brief summary of the statistical
        analysis of this trial.  You'll hear a good deal more about
        this later from Joe Quinn, but just to briefly tell you
        what the statistics were.  Using the log-rank test, the 2-year mortality reduction from hydralazine and nitrate
        compared to placebo was .0279, and the risk ratio .7.  And
        as you can see, the 95 percent confidence intervals did not
        overlap 1.
                 When the Cox model was employed, using the
        three variables that were chosen by the FDA and its
        independent consultant to be employed to adjust the log-rank test, the p value fell to .0168 and again, the
        confidence interval did not overlap 1.
                 Overall mortality by the log-rank test was a p
        value of .046, and the confidence interval did include 1. 
        When the Cox model was employed, that fell to .0177 and the
        confidence interval did not overlap 1.
                 DR. MOYE:  One question to clarify.  Can you go
        back to the previous slide, please?
                 DR. COHN:  Yes, sure, Lem.
                 DR. MOYE:  When you show the log-rank p value
        of .046, now say again what the threshold was that the
        investigators determined prospectively for stat
        significance here.
                 DR. COHN:  Oh, we'll get into that a good deal
        later.  I'm just showing you the raw p values with no
        intent to suggest that this has met any criteria that was
        established.  So, we'll get into that in more detail later
        on.  These are the raw numbers.
                 Now, the other major endpoints that I wanted to
        bring to your attention were the peak oxygen consumption
        and the ejection fraction.  This is the intent-to-treat
        analysis of changes in peak oxygen consumption over time in
        the two treatment arms of interest.  There was clearly a
        trend, but no statistical difference between the two.  A
        trend for the H/ISDN group to exhibit sustained improvement
        in peak oxygen consumption, which did not occur in the
        placebo arm, but none of these differences were
        statistically significant.
                 Now, V-HeFT I gas exchange was done by a
        primitive methodology that we developed ourselves and we
        put some instruments together.  There was no commercial
        instrument at that point available for use.  It was a
        mixing chamber.  It was a pretty crude way to measure peak
        oxygen consumption.
                 V-HeFT II, that I'll show you in a moment, was
        carried out with modern technology with breath-by-breath
        gas exchange data, so that I have more confidence in the
        V-HeFT II gas exchange data.
                 However, the protocol said that exercise tests
        would only be included for analysis if they were terminated
        by dyspnea or fatigue.  And therefore, in the protocol
        analysis, there were fewer patients included because those
        who had orthopedic reasons, et cetera, for not finishing an
        exercise test were excluded.
                 When we did that, the data looked pretty
        similar.  That is, the green line, which is H/ISDN,
        exhibited some improvement, which seemed to be at least
        unchanged or improved over time.  The placebo group in blue
        exhibited what was a trend toward a decline.  And one time
        point, at 1 year, exhibited a significant p value of less
        than .05 for the improvement of exercise performance in the
        H/ISDN group compared to the placebo group.
                 That might be shown even a little more clearly
        on this next slide, in which we have done an analysis
        looking at the changes in exercise performance by groups. 
        So, this represents in the placebo group on the left and
        the H/ISDN group on the right all patients who reached 1
        year after randomization and what their exercise tests
        showed.
                 First of all, there were more people who died
        in the placebo group.  This has already been pointed out. 
        So, this excluded them from a repeat exercise test, and
        more were excluded in the placebo arm.  
                 Then we've looked at three different levels of
        peak oxygen consumption, using .07 ml per kilogram per
        minute as the dividing point because the mean increase in
        the H/ISDN group was 0.7 at 1 year.
                 You can see that in purple are those whose
        exercise performance worsened over that 1-year period of
        time, and there were fewer here than here.  
                 In yellow are those whose exercise performance
        stayed the same between the two, and there were more people
        in this group than in this group.  
                 In this top bar are those whose exercise
        performance improved over that period of time, and there
        were more here than there were in the placebo group.  And
        these are the ones who, for administrative reasons, had
        missing data and they were equal in the two treatment arms.
                 By a chi-square analysis of these two
        distributions it's significant at the p .024 level.
                 Now, the ejection fraction changes were very
        dramatic and consistent.  That is, H/ISDN produced a
        significant and sustained improvement in ejection fraction. 
        These are all measured by radionuclide techniques
        sequentially.  In contrast, the placebo group exhibited no
        improvement and a progressive decline over time, which did
        not occur in this group.
                 I personally view the sustained improvement of
        ejection fraction as a structural alteration in the left
        ventricle with reduction of the remodeling process, which
        appears to progress in the placebo group.
                 Now, this slide adds the Prazosin group to this
        analysis.  The Prazosin group now is in blue and the
        placebo group in yellow.  You can see that these two track
        together, and there was a progressive decline of ejection
        fraction in both groups, indicating that this vasodilator,
        Prazosin, did not favorably affect the structure remodeling
        process in the left ventricle, whereas this vasodilator,
        H/ISDN, did.
                 This indeed tracks directly with the mortality
        results that I've shown you before, and we have data that I
        won't have time to go into to suggest to you that the
        changes in ejection fraction are indeed very powerful
        predictors of the change in mortality in the individual
        patient groups.
                 Well, when we completed V-HeFT I, there had
        been also the publication of data from the CONSENSUS study
        done in northern Scandinavia, in class 4 heart failure,
        using Enalapril as the treatment option.  That study
        eventually led to the approval of Enalapril for mortality
        reduction in heart failure.  And that was a 1-year trial,
        so that at the end of 1 year, in CONSENSUS, this was the
        mortality in the placebo group, very high because these
        were class 4 heart failure patients, and this was the
        mortality in the Enalapril group at 1 year, and that
        represented a 31 percent reduction.
                 When we looked at the V-HeFT data in terms of
        1-year data, this was the reduction from 20 percent to 13
        percent which represented a 38 percent reduction in
        mortality.  We thought that these two reductions were quite
        comparable, but this was indeed a very different patient
        population than V-HeFT and we therefore asked the question,
        would Enalapril have the same beneficial effect, or greater
        beneficial effect in mild to moderate heart failure as did
        hydralazine and isosorbide dinitrate in V-HeFT I, and that
        was the basis for the design of V-HeFT II.
                 These were the survival curves from V-HeFT II,
        Enalapril in green, H/ISDN in yellow, and you can see that
        there was a clear trend for improved survival with
        Enalapril, compared to hydralazine and isosorbide
        dinitrate.  
                 This is the statistical analysis in brief of
        that difference by log-rank test, and a two-sided p value
        here.  The p was .017 for the 2-year mortality difference
        between the two, favoring Enalapril, with a risk ratio of
        1.46.
                 The overall mortality difference did not
        achieve statistical significance, .0828, but a clear trend
        for a favorable effect of Enalapril compared to H/ISDN. 
        But here the confidence intervals overlap 1.0.
                 The other endpoints, again, in V-HeFT II are
        striking.  This was the intent-to-treat changes in oxygen
        consumption during exercise, and once again, H/ISDN
        exhibited a modest but sustained improvement in peak oxygen
        consumption, certainly for the first two years, and at
        least three time points these increases, when compared to
        the changes with placebo, were statistically significant --
        not placebo -- Enalapril, I'm sorry, were statistically
        significant.  At no time point during follow-up did
        Enalapril produce an improvement in peak oxygen
        consumption.  In fact, oxygen consumption tended to decline
        over time.
                 Now, this was the intent-to-treat analysis, but
        the protocol analysis, again, defined the changes to be
        identified only in patients who stopped exercising for
        dyspnea or fatigue, and this is the protocol analysis,
        showing pretty much the same thing, that there was a strong
        trend for an improvement with H/ISDN and not with
        Enalapril.  These were the statistically significant
        points.
                 I must emphasize to you that at 3 months and at
        6 months, which represents the time frame for which the FDA
        has all existing data on changes in exercise and heart
        failure therapy, H/ISDN exhibited significant improvement
        in peak exercise capacity compared to Enalapril.  I think
        that if the study therefore had been terminated at 6
        months, as have most other exercise studies, there would
        have been no question that this therapy was more effective
        than the ACE inhibitor in symptom relief or exercise
        performance in heart failure.
                 Now, once again, the ejection fraction changes
        were very striking with both therapies.  That is, both
        Enalapril in green and H/ISDN in yellow produced a sizeable
        and sustained improvement in ejection fraction.  In fact,
        at 3 months the increase in the H/ISDN group was greater
        than the increase in the Enalapril group.  Thereafter the
        two were similar, suggesting that both interventions
        favorably affect the remodeling process in the left
        ventricle.
                 Now, we were struck when we completed V-HeFT
        II, and we had the same treatment arm in both trials --
        that is the H/ISDN arm was exactly identical and the
        therapy was identical in the two trials.  The survival
        curves for these two treatment arms were superimposable. 
        That implied to us that there must have been some stability
        in this response since it was so reproducible.
                 Now, this of course then comes to the placebo
        arms because we did not repeat a placebo in V-HeFT II and
        therefore, we are dependent on the placebo group in V-HeFT
        I.  I have given you a list here of the so-called placebo
        groups in more recent heart failure trials.  I have given
        you data on the number of deaths in these trials, in the
        placebo arms, the duration of follow-up, and the use of
        what may be critical co-therapy.  That is, the use of
        nitrates and the use of ACE inhibitors.
                 In V-HeFT I there were 120 deaths, so this is a
        rather robust sample.  The follow-up was 2.3 years.  None
        of the patients in the placebo arm received nitrates, and
        none of them received ACE inhibitors.  This is a true
        placebo group, added to digoxin and diuretic therapy.
                 CONSENSUS, that I have already alluded to, had
        only 55 deaths in the placebo arm.  The follow-up averaged
        only 0.5 years.  45 percent of those patients were treated
        with a nitrate, which obviously potentially contaminates
        the placebo group.  
                 In the SOLVD trial, which is the largest
        clinical experience in heart failure trials, there were 510
        deaths in the placebo arm, and a follow-up of 3.4 years,
        which makes this a very robust placebo group.  But it isn't
        a placebo group because 45 percent of these patients were
        treated with nitrates chronically, and 23 percent in the
        placebo group were given ACE inhibitors as drop-in therapy. 
        So, this is certainly not a placebo group.
                 Now, the more recent trials, PROMISE, which
        exhibited an adverse effect of milrinone in heart failure,
        had 127 deaths in the placebo group, an average follow-up
        of only 0.5 years.  But 59 percent of that placebo group
        was treated with nitrates, and essentially all of them at
        least were by protocol on ACE inhibitor.  We don't have the
        actual data in the paper.
                 The Vesnarinone trial, which was not replicated
        by the more recent VEST study, have only 33 deaths in the
        initial Vesnarinone mortality trial in the placebo arm. 
        The follow-up was only 0.5 years.  We don't know about
        nitrates, but 90 percent of the placebo group were on ACE
        inhibitors.
                 The more recent Carvedilol American data that
        you'll be reviewing later this morning, in the placebo
        group there were 31 deaths.  As you know, the follow-up was
        only 0.5 years, but once again, 32 percent of them were
        receiving nitrates and essentially all of them were
        receiving an ACE inhibitor.
                 So, this is to point out to you that we will
        never again have a placebo arm comparable to V-HeFT I
        because it is ethically indefensible to any longer treat
        patients without an ACE inhibitor, and we would like to
        suggest that after today's meeting it would be equally
        indefensible to treat them without a nitrate along with
        hydralazine.
                 Well, if we can use that placebo arm, then, as
        a comparator, we can put a plot of the five treatment arms
        from V-HeFT, and in fact this analysis was recommended by
        the FDA for us to do.  So, this is in response to their
        raising the issue about comparing the V-HeFT I placebo
        group here in red with Enalapril in blue and with the two
        hydralazine-isosorbide dinitrate curves in yellow.
                 Now, a 2-year endpoint was indeed a pre-study
        endpoint, so we have dropped a vertical at 2 years in the
        placebo arm, and discovered this is the mortality at 2
        years and we put a horizontal line over to this mortality,
        which is about 65 percent.  
                 Then we determined at what time point would you
        reach that same mortality if you had instead been treated
        with hydralazine and isosorbide dinitrate, and these two
        curves, which were just superimposed, show you that there
        is a prolongation of life by an average of about 10 months.
                 If instead we had used Enalapril, the
        prolongation of life would have been longer, at maximum
        probably another 8 months.  Obviously the effect is more
        than 50 percent of this effect, and this effect is enhanced
        by the fact that there was a little blip on that Enalapril
        curve there, but be that as it may, it's clear that
        Enalapril had a more favorable effect than did hydralazine
        and isosorbide dinitrate.  But both are very importantly
        better than the placebo or Prazosin arms shown here.
                 Well, in summary, then, I've told you that
        mortality is reduced by H/ISDN, that there is a strong
        trend for improved exercise tolerance by H/ISDN, and that
        there is sustained improvement in ejection fraction with
        H/ISDN.  
                 Now, a number of statistical issues have been
        raised by the FDA, and I'll now turn the podium over to Joe
        Quinn, who will address some of these issues.  Joe?   
                 DR. QUINN:  Thank you, Dr. Cohn, and good
        morning to everyone.
                 I would like to discuss several important
        statistical issues that have been raised by the agency that
        potentially impact the interpretation of the nominal p
        values in the application.  
                 The first issue is the impact of the interim
        analysis.  This slide summarizes the interim results of the
        overall survival time that were provided to the V-HeFT I
        Operations Committee.
                 Note that even though the protocol specified --
        sorry.  This slide summarizes the interim results of the
        overall survival time that were provided to the V-HeFT I
        Operations Committee.  Note that even though the protocol
        specified a one-sided test hypothesis, the p values shown
        are two-sided p values, as the committee wanted to be
        conservative in their decisionmaking.
                 There were four interim analyses that were
        conducted using the O'Brien-Fleming criteria.  These are
        shown on the right-hand side with the critical values.
                 Additionally, there were four interim analyses
        conducted for administrative purposes.
                 The columns represent the protocol-specified
        ways of comparing the arms.  Overall tests between the 3
        curves, using a 2 degree of freedom test, a combined active
        versus placebo arm, and the two pairwise comparisons of the
        active arms to placebo.
                 Note that the first three looks at the data
        were performed using an overall test.  A trend was observed
        in February of 1983 comparing the best arm, which was
        H/ISDN, to the worst arm, placebo.  It was after this
        analysis that the Operations Committee unblinded
        themselves.  
                 In May of 1983 it is important to note that a
        significant difference using the O'Brien-Fleming stopping
        boundary was observed between H/ISDN and placebo.  However,
        the trial continued without change.  The majority of the
        protocol specified comparisons were made after the
        significant interim result was established, pointed out in
        this area.
                 Note that even though the overall survival time
        was used for this analysis, the significant results
        obtained in May of 1983 were more similar to a 2-year
        endpoint.  
                 The O'Brien-Fleming method was not the pre-specified method in the protocol but was used after the
        method was published in 1979 as it was easier to implement
        than the Canner method that was a pre-specified method.
                 The next slide I'm going to show you is not
        included in the committee packet of slides, nor has it been
        shared with the FDA, due to the recent completion of this
        simulation, but we feel it shows strong, supportive
        information that also assesses the sensitivity of the
        O'Brien-Fleming method that was used.  
                 This slide summarizes the simulation of an
        interim analysis using the protocol specified Canner
        method.  The results of this simulation support the
        findings of the O'Brien-Fleming method, indicating a
        superior mortality benefit for H/ISDN over placebo in May
        of 1983, as well as in August 1984. 
                 The critical p value that was used for this
        simulation was a .0125 for the comparison of H/ISDN to
        placebo, a .0125 for Prazosin versus placebo, and .025 for
        the combined active versus placebo.
                 There were several reasons that the committee
        did not stop the study after the significant interim
        finding in May of 1983 was observed.  Importantly, the
        impact of the differences in the baseline characteristics
        of the patients upon survival had not yet been assessed,
        and the committee wanted to establish the length of benefit
        of the H/ISDN effect.
                 In summary, there was a statistically
        significant interim analysis in May of 1983, according to
        the O'Brien-Fleming stopping criteria.  The study continued
        beyond May of 1983 to investigate the length of benefit of
        effect.  The protocol-specified secondary analyses -- that
        is, the Cox model -- were justified based upon the
        significant interim results.  As the May 1983 analysis met
        the stopping criteria, no penalty is required for the
        interim analyses that were conducted after this May 1983
        finding.  
                 The next issue is the multiple treatment arm
        comparisons.  As previously shown, the interim testing was
        conducted in a protected fashion.  First, the overall test
        of the three treatment arms, using a 2 degree of freedom
        test, was employed.  Secondly, the best versus the worst
        arms were compared in February of 1983, and again in May of
        1983.  Only after a significant result was obtained in May
        of 1983 were the combined active versus placebo arms and
        pairwise comparisons made.  
                 We would suggest that after significant
        differences were established in May of 1983, no alpha
        penalty is warranted for the protocol-planned comparisons
        performed subsequent to this time.
                 The next issue is the stepwise approach to the
        analysis, that is, a non-significant log-rank test, then a
        Cox model analysis.  The significant log-rank interim
        analysis in May of 1983 justified the protocol-specified
        secondary analysis, the Cox model, without alpha penalty. 
        The analysis of a covariance method gave a more precise
        estimate of the true treatment effect, especially for
        overall survival where the estimate of effect is more
        variable because of the small number of patients in the
        trial after 3 years.
                 The next issue is the imputation of missing
        covariate values.  There were a total of 459 patients in
        the placebo and H/ISDN treatment arms in V-HeFT I.  There
        were 51 of 459 patients that were missing either baseline
        ejection fraction or baseline peak O2, two of the
        covariates selected by Dr. Packer as a consultant to FDA.
                 This slide shows the baseline mean values of
        ejection fraction and max oxygen consumption by survival
        status.  There was a consistent trend independent of
        treatment group showing that patients dying during the
        study had a lower baseline EF and lower baseline max O2
        than those alive at the end of the study.
                 This slide shows similar data in a slightly
        different fashion.  This slide shows the cumulative
        mortality by baseline ejection fraction and baseline oxygen
        consumption during peak exercise.  The patients with the
        lowest ejection fraction and lowest oxygen consumption had
        the highest mortality during the study.
                 There were incremental advantages in total
        mortality observed by baseline ejection fraction and oxygen
        consumption, with patients having the higher baseline
        ejection fraction and higher baseline oxygen consumption
        having the lowest mortality.  
                 This next slide summarizes a simulation
        analysis performed by Dr. Jim Hung at FDA, showing
        alternative methods for imputing missing values of baseline
        ejection fraction and maximum oxygen consumption.  The
        first row of this table shows the results when the maximum
        non-missing value is used to impute the missing values for
        the patients that died, and the minimum non-missing value
        is used to impute the missing values for the patients that
        survived.  This approach may not make sense, given the data
        which I have just shown to you, and what we know about the
        trials regarding the prognostic significance of ejection
        fraction in oxygen consumption upon survival.  
                 The second row shows the results if one uses
        the mean value to impute the missing values for all
        patients with missing ejection fraction or max oxygen
        consumption, regardless if they died during the trial. 
        This is the method that most closely resembles the approach
        used by Dr. Lloyd Fisher for the analysis submitted in our
        application.  This method leads to a p value of .016 in the
        Cox model for overall survival and a p value of .013 for 2-year survival.
                 The third row shows the results obtained if one
        uses the minimum non-missing value for ejection fraction in
        max O2 as the imputed value for those patients that died
        during the trial.  And the maximum non-missing value of
        ejection fraction and max O2 for those that did not die
        during the trial.
                 Based upon the data that I have just shown you,
        and based upon what we know about the prognostic
        significance of ejection fraction and oxygen consumption
        from other trials, this method has strong intuitive appeal. 
        Using this method to impute the missing 51 covariate
        values, one obtains a p value of .007 for the overall
        survival, and .01 for the 2-year survival.  The true p
        value probably lies somewhere in between .016 and .007 for
        the overall survival and probably somewhere between .013
        and .01 for the 2-year survival.
                 Finally, I would like to point out regarding
        the last column, labeled log-rank/Cox, these columns
        indicate the simulation results for the incremental
        increase in the p value for conducting the Cox analysis
        after a non-significant log-rank test.  As previously
        mentioned, the statistically significant log-rank test in
        the May 1983 interim analysis provided a rationale for
        conducting the Cox analysis without an adjustment in the p
        value for this approach.
                 In summary, the sensitivity analysis conducted
        by Dr. Hung indicates a range of nominal p values,
        depending upon the method used for imputing the missing
        covariates.  Use of a minimum value for deaths and maximum
        value for survivors is reasonable, given the observed
        findings and what we know about the prognostic significance
        of these covariates.  Use of a mean value may lead to a
        more conservative p value, especially for overall survival.
                 The next issue is the two protocol-specified
        primary endpoints.  There was a 33 percent reduction in
        mortality through 2 years, and a 27 percent reduction in
        overall study mortality for H/ISDN treated patients.  The
        one-sided 95 percent confidence intervals indicate the
        H/ISDN risk reduction is consistent with the range of
        observed findings.  The observed risk reduction at both
        time periods was consistent and correlated, and both
        findings represent different point estimates of one
        endpoint, that is, survival.
                 In summary, the consistent risk reduction was
        observed at 2 years and overall study.  The protocol
        specified a valuation at two time points to assess the
        length of benefit of effect.  The estimate of effect may be
        influenced by the sample size at 2 years, and at the end of
        study, and it may be reasonable to consider survival data
        as one endpoint, having two point estimates of effect for
        the modest alpha penalty imposed upon the nominal p values.
                 The last issue is the issue of the replication
        of the study findings.  There are three questions that have
        been suggested by the agency that must be addressed for
        this issue.  Would H/ISDN have beaten placebo if it had
        been studied in V-HeFT II?  And what is an appropriate
        placebo group to use for this comparison?  And is the point
        estimate of the effect size for H/ISDN less than half the
        effect size of Enalapril?
                 Because of ethical concerns, the demonstrated
        mortality benefits observed in V-HeFT I were not
        replicated.  However, the agency has suggested analyses
        that might be supportive of the mortality benefit and the
        following is presented as supportive information.  We
        strongly feel that the randomized concurrent control arm of
        V-HeFT I is the appropriate basis for the mortality
        benefit.
                 It has been proposed by the agency that the
        placebo arm from the SOLVD treatment study may be an
        appropriate arm for comparison.  This slide shows the risk
        ratio for mortality relative to Enalapril for SOLVD
        treatment, placebo, and V-HeFT II H/ISDN.  When the H/ISDN
        effect is compared to this placebo, there is no observed
        difference in the risk estimates.  This is true at both the
        2-year and the overall time points.
                 However, this placebo arm is flawed for purpose
        of making this comparison, of the following reasons.  This
        study allowed the active use of vasodilators and nitrates
        and the study also allowed open-label use of ACE
        inhibitors.  This placebo arm is therefore not an adequate
        control for making this comparison.  And one would not
        expect to observe a difference between H/ISDN in such an
        arm.
                 A more appropriate control arm is the placebo
        arm from V-HeFT I.  The placebo arm from V-HeFT I allowed
        only digitalis and diuretic use.  Once V-HeFT I was
        completed, it was no longer ethical to use this control arm
        in this patient population.  Use of the V-HeFT I placebo
        group as a control group for V-HeFT II makes sense, given
        the similarity of the patient populations studied and the
        conduct and handling of both trials.
                 As previously shown by Dr. Cohn, this slide
        shows the survival profile for H/ISDN treated patients in
        V-HeFT I and V-HeFT II.  It is clear that this profile is
        very similar, but this does not allow one to conclude that
        the risk reduction for H/ISDN is replicated in V-HeFT II. 
        To do that, one must also consider the data from the second
        arm of that trial, Enalapril, and how each arm would have
        performed relative to a placebo group, had there been one.
                 This slide shows the risk reduction and the 95
        percent confidence intervals for V-HeFT I and V-HeFT II, as
        well as the risk reduction for Enalapril compared to V-HeFT
        I placebo, and H/ISDN from V-HeFT II compared to V-HeFT I
        placebo.  
                 It is important to note the following.  The
        risk reduction observed for H/ISDN and V-HeFT I, .73, is
        consistent with the observed risk reduction for H/ISDN and
        V-HeFT II, compared to V-HeFT I placebo, .75.  There is a
        strong suggestion of an overall Enalapril benefit in V-HeFT
        II, even though the 95 percent confidence interval includes
        1.
                 The risk reduction observed for Enalapril,
        compared to V-HeFT I placebo, .61, is consistent with the
        expected conclusion of an Enalapril survival benefit. 
        Importantly, the point estimate of the H/ISDN risk
        reduction, .75, is not less than half of the point estimate
        of Enalapril, when both are compared to a common placebo. 
        Also, the upper bound of the Enalapril effect overlaps the
        point estimate of the H/ISDN effect, as does the lower
        bound of the H/ISDN effect overlap the point estimate of
        Enalapril. 
                 In summary, V-HeFT I was the only study with a
        true placebo arm.  The Enalapril survival benefit versus
        V-HeFT I placebo was consistent with the expected survival
        benefit of Enalapril.  The H/ISDN survival benefit from
        V-HeFT I was replicated in V-HeFT II when compared to the
        V-HeFT I placebo group, and the point estimate of the
        V-HeFT II H/ISDN survival effect was not less than half the
        effect size of Enalapril, when compared to a V-HeFT I
        placebo.
                 In conclusion, it is reasonable to expect
        little or no impact upon the nominal p values due to the
        issues described.  The extent of the alpha penalty does not
        impact the interpretation of the observed survival benefit
        for H/ISDN in V-HeFT I.  And it is reasonable to conclude
        that the H/ISDN survival benefit was replicated in a second
        study.
                 And now Dr. Jay Cohn will provide a clinical
        wrap-up to the presentation.
                 DR. COHN:  Well, a number of other endpoints
        were monitored in V-HeFT I and II and time won't allow us
        to go into all these, but a few of them have been
        specifically addressed by the agency, and I'll try to
        provide those data.  In V-HeFT I and V-HeFT II, we measured
        cardiac hospitalizations as well as we could.  Quite a
        different population because these were VA centers and the
        criteria for admission to a VA hospital are quite different
        from those to private hospitals.
                 Quality of life was assessed in both trials,
        but I must point out to you that in 1979 when we planned
        V-HeFT I, there were really no appropriate quality of life
        instruments that could be used, so this was truly not a
        quality of life assessment.  We did use a form in V-HeFT II
        that I will show you in a moment.  It was never validated. 
        It has not been re-used.  We have subsequently developed a
        Minnesota Living with Heart Failure Questionnaire, which
        was not employed in all the centers in V-HeFT II.
                 We monitored heart size, we monitored
        echocardiograms.  We did Holter monitoring, and we measured
        plasma norepinephrine levels, and time will not allow me to
        go into these endpoints.
                 The time to death or hospitalization is shown
        here because the agency asked about hospitalizations.  This
        is the V-HeFT I data showing time to death or
        hospitalization, and you can see there was a clear trend
        for the H/ISDN group to fare better than the placebo group,
        but this was not statistically significant.
                 This is the analysis of the V-HeFT II, that is,
        time to death or hospitalization.  In V-HeFT II, and as you
        might predict, there was a more favorable effect of
        Enalapril compared to H/ISDN, largely reflecting the
        mortality difference because when we look at just the time
        to first hospitalization for any reason in V-HeFT II, the
        two curves for Enalapril and H/ISDN superimpose and there
        is no difference at all between them.
                 If one accepts, then, that Enalapril has a
        significant impact on hospitalizations and reduces it, as
        it has in other studies, one might conclude that H/ISDN is
        not different from Enalapril in that regard.  
                 This is the quality of life assessment we did
        in V-HeFT II, called a Heart Condition Assessment Score. 
        This is the changes over time, an increase being an
        improvement in quality of life, a decrease being a decrease
        in quality of life, and there is no striking difference
        between H/ISDN and Enalapril.  
                 At the first time point, 3 months, where the
        agency has almost all of its data on quality of life in
        heart failure and the effects of therapy, H/ISDN exhibited
        a significant increase.  Enalapril did not.  That p value
        was less than .05 at 3 months.
                 Thereafter, quality of life declined
        progressively in both groups, which tells you a little bit
        about the natural history of heart failure.  At all time
        points, though, there was a greater decline in quality of
        life in the Enalapril group than in the H/ISDN group,
        suggesting a trend for more favorable effect of H/ISDN,
        consistent with the trends on exercise performance.
                 Now, the safety of these two drugs I won't go
        into.  You have it in your document, all the side effect
        data.  The safety has been well characterized.  We know,
        and it has been confirmed, that H/ISDN causes headache and
        that is reduced when the dose is reduced.  We know that
        Enalapril causes cough and that clearly appeared in the
        database.
                 There were essentially no instances of lupus in
        V-HeFT I.  There were two possible cases in V-HeFT II, but
        it's clear that the incidence of lupus as a complication of
        hydralazine is exceedingly uncommon in this patient
        population.
                 Now, the issue of nitrate tolerance has been
        raised repeatedly, both in the clinical arena and by the
        agency because of the well-known tolerance that develops to
        continuous nitrate administration in their treatment of
        angina.  The mechanisms for this nitrate tolerance have in
        the past not been clarified.  There are many mechanisms
        that have been suggested, but there is recent and perhaps
        the most exciting data of all, the role of hydralazine as
        an inhibitor of nitrate tolerance.
                 It appears that when we serendipitously put
        these two drugs together in the late 1970s, not knowing at
        all what the interaction was but knowing that they were
        both vasodilators, we did something that proved to be
        remarkably effective, and that is, we added to nitrate a
        nitrate tolerance inhibitor.  I'll show you just briefly
        the data on that issue.
                 It has been well established in a number of
        laboratories, laboratories of Munzel and Harrison and
        Besange, that nitrate tolerance is associated with the
        generation of superoxides at the endothelial surface. 
        These superoxides chew up nitric oxide and thus inhibit the
        nitric oxide effect which characterizes the hemodynamic
        response to nitrates.  
                 This is just one slide from a paper by Winslow
        that was published in the Journal of Clinical Investigation
        last year, in which superoxides are measured in response to
        NADH addition as a substrate.  This is carried out in
        ground-up aortas from rabbits, who were either not treated
        with nitroglycerin or treated with nitroglycerin, or
        treated with nitroglycerin in addition to hydralazine for 3
        days before the aortas were taken out and ground up.
                 You will notice that this is the superoxide
        production in response to NADH in a controlled animal that
        received neither nitroglycerin or hydralazine.  This second
        black bar is the increase that is identified when the
        animal had been treated for 3 days with nitroglycerin, an
        excess by about two or three-fold of the amount of
        superoxide that is produced in the vasculature.
                 When hydralazine was added to nitroglycerin in
        the treatment of these animals for 3 days, there was no
        excess of superoxide produced, implying that the
        hydralazine had prevented the generation of the superoxide
        which causes nitrate tolerance.
                 Now, the in vivo documentation of this
        combination has been well established.  This is a study
        performed by Dr. Ho-Leung Fung, who is in the audience in
        case there are any questions raised about this, in which he
        took rats with myocardial infarction who had an elevated
        left ventricular end diastolic pressure and infused
        nitroglycerin continuously.
                 In open circles is the response of the left
        ventricular end diastolic pressure to nitroglycerin.  It
        comes down and then gradually recovers, despite the fact
        that the nitroglycerin infusion is continued.  This
        recovery to pre-treatment levels implies nitroglycerin
        tolerance, the hemodynamic effect of the nitroglycerin.
                 When in fact he added hydralazine to the
        regimen, which in itself did not change LVEDP, the fall was
        comparable with the nitroglycerin but now the nitroglycerin
        effect was sustained over 10 hours.  This is a significant
        inhibition of the tolerance that developed in the
        nitroglycerin-alone treated rats.  
                 And then to bring this to the clinic, Dr. Uri
        Elkayam and his colleagues in Los Angeles -- and Uri is
        also in the audience in case there are any questions -- did
        the same trial in humans with heart failure.  Infusion of
        nitroglycerin in these patients with heart failure produced
        a decline in the pulmonary capillary wedge pressure and
        then when the nitroglycerin infusion was continued, the
        wedge pressure rose progressively, implying tolerance to
        the hemodynamic effects of nitroglycerin.
                 When hydralazine was co-administered with the
        nitroglycerin, the favorable effect of nitroglycerin on
        pulmonary-capillary pressure was sustained.  So, there
        appears to be rather persuasive evidence now that
        hydralazine is a potent antioxidant which inhibits the
        tolerance that may develop to nitroglycerin or to
        isosorbide dinitrate.
                 Now, I am not willing to accede that
        hemodynamic tolerance is necessarily also implied, that
        there is tolerance to the anti-remodeling effect of
        nitrates on left ventricular function.  I think these must
        be viewed as separate endpoints, and we can't assume that
        one is related to the other.  But I think that this is
        clear evidence that whatever tolerance might develop during
        chronic administration of isosorbide dinitrate should very
        much be inhibited by the co-administration of hydralazine.
                 Well, I alluded at the beginning to the fact
        that the guideline committees have approved this therapy
        already and I just remind you, and you have in your
        briefing document the details of these guidelines, and in
        fact many members of this committee have served on these
        guideline committees.  There are three identified here. 
        That is, the guidelines issued by the American College of
        Cardiology and the American Heart Association for the
        treatment of heart failure, the guidelines issued by the
        Agency for Health Care Policy Research, and the guidelines
        for heart failure treatment issued by the World Health
        Organization.
                 All of these guidelines recommend for therapy
        of heart failure digoxin and diuretics, the use of ACE
        inhibitors, and the use of hydralazine and isosorbide
        dinitrate in patients who are not taking an ACE inhibitor. 
        They do not suggest this should replace ACE inhibitors,
        that this should be used in patients who do not take those
        drugs.
                 Well, I just would like to finish up by putting
        in context what I have learned from these V-HeFT trials
        because this has changed the paradigm.  We used to think
        that heart failure was a syndrome in which there were many
        endpoints, all of which should be in concert.  I think we
        now know that they are distinct, and that the progressive
        process in the left ventricle with dilatation, which we
        call remodeling, and a progressive fall in ejection
        fraction leads to premature death from arrhythmias or pump
        failure, and this process may continue and progress to
        death in the absence of symptoms.
                 In fact, the SOLVD trial, the SOLVD prevention
        trial, was initiated to identify patients out here with a
        low EF and no symptoms.  So that it is quite possible to go
        through this whole disease without symptoms.  The presence
        of symptoms relates largely to noncardiac factors which may
        be variably stimulated by this process in the left
        ventricle, and may include neurohormonal activation and
        multiple other factors as well.
                 Most of the data that have been previously
        reviewed by the FDA for treatment of heart failure for
        relief of symptoms have involved short-term studies in
        which symptom relief is really a short-term goal of
        therapy.  In contrast, if one is interested in this process
        leading to death, one must do a long-term trial and one
        must used therapies to interfere with this process that may
        be quite separate from therapies aimed at relieving
        symptoms.
                 So, I currently view the management of heart
        failure really with two different goals in mind.  One is
        short-term symptom relief, and for that we often use -- we
        do use -- diuretics and vasodilator may favorably affect
        short-term symptoms by producing a favorable hemodynamic
        effect.  And we even use occasionally positively inotropic
        drugs like dobutamine and milrinone in order to have a
        favorable effect on hemodynamics and on symptoms, despite
        the fact that we know that these drugs shorten life
        expectancy, apparently, and some of these drugs have no
        effect on life expectancy and some may shorten it.  So that
        there is no relationship between the favorable effect of
        these drugs on symptoms and the potential for therapy to
        alter the long-term course of the disease.  
                 From what we now know, progressive left
        ventricular dysfunction can be inhibited and therefore
        mortality reduced by ACE inhibitors, by hydralazine and
        isosorbide dinitrate, I believe by beta-blockers -- and you
        are going to be dealing with that contentious issue this
        afternoon -- and perhaps by other neurohormonal inhibitors
        which can alter the milieu and influence the rate at which
        the left ventricle remodels, yet to be determined out here.
                 But I think we have reached the point now where
        we have to identify specific endpoints for a therapeutic
        approach.  The only agent which appears on both sides of
        these columns is hydralazine and isosorbide dinitrate
        because it does relieve symptoms and improves exercise as a
        potent vasodilator, and it also inhibits the progressive
        remodeling process in the left ventricle.
                 Well, in summary, then, I hope we have been
        able to convince you, Mr. Chairman, that there is a strong
        basis for approval of BiDil for congestive heart failure. 
        That is, that the combination of hydralazine and isosorbide
        dinitrate exhibits a survival benefit compared to placebo;
        that it exhibits a strong trend for improved exercise
        tolerance versus both placebo and versus Enalapril and
        V-HeFT II; that it produces a sustained improvement in
        ejection fraction, which I believe means that it is
        inhibiting the remodeling process and it also confirms the
        long-term effect of these two vasodilators; that this
        combination therapy has a well-established rationale, even
        more well-established by the recent data relating to
        nitrate tolerance; that the safety of this combination is
        well-established; that it is already widely recommended as
        a treatment option in all the guidelines issued for the
        management of heart failure; and that indeed the practicing
        physicians require prescribing information to properly
        utilize this remarkably effective therapy.  
                 Thank you very much.
                 DR. MASSIE:  Thank you very much, Jay.  
                 The way I think we should proceed from here is
        first open up this presentation to questions from the
        committee and our consultants.  We are going to lead off
        with our reviewers, as we usually do, and our consultants,
        and if the reviewers from the FDA want to ask some
        questions at that point, that would also be appropriate. 
        Then we'll ask the reviewers from the FDA for comments and
        then we'll proceed on to the questions.  
                 So, why don't we start.  Lem, do you want to
        start, since you had some statistical questions?
                 DR. MOYE:  Sure.
                 In nowhere as part of the slide presentation
        that we saw today did I see the -- and if this was here and
        I missed it, I apologize, but I don't think I saw the log-rank analyses which led to the p value of 0.093.  And I
        wondered if you could comment on that.
                 DR. QUINN:  I think you are referring to the
        two-sided log-rank test that was in the original
        application?
                 DR. MOYE:  That's right.
                 DR. QUINN:  Well, that has been presented as
        the one-sided p value that corresponds to that two-sided
        test, as the protocol specified the one-sided p value as
        the appropriate method.
                 DR. MOYE:  And so the one-sided p value is what
        precisely?
                 DR. QUINN:  Can I go back to that slide?     It would be the one from Dr. Cohn's presentation of
        the summary of the V-HeFT I survival.
                 DR. MOYE:  That's where I think I first asked
        the question.  It's 0.04.
                 DR. COHN:  It's .046, I think.
                 DR. MOYE:  Okay.  
                 Now, the threshold for significance, which was
        prospectively specified by the investigators, was at, again
        one-sided, 0.025.  Is that right?
                 DR. QUINN:  Well, it's difficult to interpret
        the protocol actually.  The protocol suggested that
        different alternatives could be employed, depending upon
        the number of comparisons that were made.  And the protocol
        suggests that if the combined active versus placebo arm was
        compared, as well as the two individual active arms to
        placebo, then that the individual active arms to placebo
        could be compared at the .0125.
                 However, the protocol doesn't necessarily lead
        one to believe that all those tests would be conducted and
        the pairwise comparisons could also have been tested at
        .025 and the rationale that I'm trying to make is that the
        interim analysis of May 1983 that met the O'Brien-Fleming
        stopping criteria, was the significant log-rank test found
        for the trial.
                 DR. MOYE:  But since the trial was allowed to
        continue, I think it's also admissible that that might not
        be the definitive p value because of course, as you get
        these multiple p values, as you go through the interim
        analyses, one could choose any p value they wanted and
        continue to go through the trial, amassing additional p
        value.  There is a problem with that approach, right? 
        Okay.
                 One other question.  The protocol is actually
        quite laudatory of the log-rank test.  I will not read the
        individual statements from the protocol, but there are I
        think two locations where they mention the superiority of
        the log-rank test and that it is distribution-free, and I
        think they go so far as to say that one of the best tests
        available to identify small differences between treatments
        is the log-rank test.
                 Yet, now there is a good deal of emphasis on
        the Cox analysis approach.  I could only find one brief
        mention of the Cox analysis approach in the protocol and if
        I compared statements about the log-rank versus statements
        about the Cox, my view would be that the investigators were
        hanging their hopes on the log-rank and not the Cox.  Yet,
        we see a good deal of analyses today centered on the Cox
        progression analysis approach.
                 DR. QUINN:  Well, the survival curves become
        more variable at later time points of the trial, and the
        Cox model helps to partition out some of that variability
        and to assess the treatment effect.
                 DR. COHN:  Yes, if I could just comment about
        that, Dr. Moye, because you have to remember, this protocol
        was planned in 1978 or 1979.  There were no data yet on
        long-term follow-up of heart failure.  So, the possible
        potency of covariates and variables in influencing
        mortality was completely unknown at that time.
                 I think that all current trials in heart
        failure are done recognizing those variables and adjusting
        for them, usually with a Cox analysis.  
                 I agree with you.  At the time this protocol
        was written, the Cox analysis was not necessarily
        identified as an important determinant, for the very reason
        that we were not very cognizant of how important these were
        going to be in influencing this ultimate survival.
                 DR. MOYE:  So, I guess the crux of the matter
        here for me is, is there ever a circumstance when the
        primary statistical prospectively stated analysis plan can
        be adumbrated, can be substituted by another analysis plan
        using another stat analysis procedure?
                 DR. COHN:  Again, I think you are entirely
        right, and that is why we have gone into this intensive
        analysis of the statistics because that question has come
        up repeatedly and we can only show you the data as they
        are.  These are the p values.  One has to interpret them as
        one chooses to do.
                 But keep in mind that this is a study designed
        20 years ago.  This was a VA cooperative study.  This was
        not designed really as a regulatory study so that careful
        selection of criteria for endpoint were not as precise as
        one would see in a protocol designed today with the goal to
        come to this committee and ask for approval.  So, one has
        to look at this a little differently than one might at a
        more recently organized mega-trial in which p values are
        clearly defined as the goals for the trial.
                 DR. MOYE:  Thank you.
                 DR. MASSIE:  Let me just read the statement I
        think that Dr. Moye was pointing out.  This is in the
        analysis method of the protocol, the PF1 on page 34, where
        it said that variables which are prognostically important
        will be identified by comparing survival curves of patients
        on different levels of baseline variables.  The life table
        regression procedures of Cox will also be used to identify
        variables that are prognostically important and to obtain
        estimates of treatment effects adjusted for any equality in
        their distribution between treatments.
                 Now, one thing that struck me on the baseline
        characteristics is there were no inequalities of those
        prognostically important variables.  Was that the case?
                 DR. COHN:  Yes.  There were no significant
        differences when one asks are there differences between the
        two groups, but of course there are subtle differences
        which may impact upon mortality that don't reach
        statistical significance when one compares the two groups. 
        It has been the usual approach in V-HeFT to look at all
        variables and not just confine oneself to variables that
        show a significant difference between the two treatment
        arms.
                 And you can see the degree of adjustment that
        was required when we switched from a log-rank test to a Cox
        analysis, albeit using now only those variables identified
        by the agency and not the variables that we had originally
        planned on using because they were preselected
        independently.
                 DR. MASSIE:  It's just that in my naivete I was
        surprised that there was such a substantial difference in
        the outcome of those analyses, despite the lack of what
        looked like even trends.  I saw a .5 difference in VO2, but
        everything else looked right-on.  I wondered how much of
        that might have been as a result of imputation of the
        missing values as opposed to --
                 DR. COHN:  Well, there were only 51 missing
        values in this whole group out of --
                 DR. QUINN:  459.
                 DR. COHN:  -- 400 and some patients, so it's
        really a relatively small number.  
                 It would probably be appropriate -- Lloyd, do
        you want to make a comment about that?  Because Lloyd has
        really spent a lot of time going over these data.
                 DR. FISHER:  Well, just that the reason you can
        get a difference is, there are papers out showing in the
        Cox model, if the Cox model with covariates holds, if it is
        appropriate -- and that is an if -- then if you leave out
        other covariates, you bias the estimated effect downward. 
        That is, I think, Piantadosi and Sam Weyend and some other
        people have published that.
                 So, perhaps the reason there is a change is
        slightly analogous to in the analysis of variance you can
        reduce your variability by taking into account factors.  It
        is not that you are correcting for baseline imbalance, but
        you have a more precise treatment estimate when you also
        take into account the other factors, and that does not
        contribute to the variability.  That would be my guess that
        that is how this happens.
                 Now, having said that, how you would actually
        prove a statement like that I am not sure, but it certainly
        can happen mathematically.
                 DR. MASSIE:  Lem, and then I thought I would
        ask Dr. D'Agostino to comment after Lem.
                 DR. MOYE:  Just one brief question.  I wonder
        if you would comment on the concerns that have been raised
        about the lack of fit of the Cox progression model.
                 DR. FISHER:  Pardon me.  About the lack of fit?
                 DR. MOYE:  The difficulty with the
        believability of the underlying assumptions required by the
        Cox regression model.
                 DR. FISHER:  Yes, I would be happy to comment
        on that because that's actually how I got involved in this.
                 Things were somewhat down the road and the FDA
        review said the fit was examined in two ways, minus log
        plots.  And also on the SAS output there was a statistic
        for fit.  One of the p values for goodness of fit was .049
        or something.
                 And I came in there and I looked at the plots
        and I said, hey, this is proportional hazards.  I knew
        that.  I mean, I looked at it.  Now, this isn't proof, this
        is Gestalt.  
                 So, what I suggested to the agency, I said,
        let's go to the randomization test.  We'll use the Cox
        statistic but because we're worried about the parametric
        assumptions, we will go to the randomization test for the
        treatment effect, which is what we did, the primary thing
        actually that I did in my analysis.
                 Before that was done that was agreed upon at a
        meeting with the agency that -- of course, the
        randomization test is always valid.  It doesn't depend on
        the assumptions.  The p value actually turned out to be
        almost exactly the same.  To be perfectly frank, even
        before we did it, I knew that would happen because I had
        seen the plots and it looked like proportional hazards.
                 But nevertheless, I think it will alleviate
        that concern with the agency.  I assume that Jim is here,
        and if the agency still has concerns about that, they can
        bring them up.  I don't think that's much of an issue here.
                 DR. MASSIE:  Ralph, do you want to help?
                 DR. D'AGOSTINO:  Well, I'm not going to help
        but I'm going to say something.
                 I guess I'm not overwhelmed with the notion
        that the protocol says a log-rank test as the major test,
        and then later on one may want to shift to a Cox.  I have
        written protocols where the analysis that we actually used
        wasn't even invented when the protocol was being written. 
        So, the notion of shifting is not too dramatic.  
                 But in this case here there is such a heavy
        reliance on the log-rank test that you sort of say that
        this is the procedure to be used, and then when they're
        shifting to the Cox, as the analysis is produced, it does
        become bothersome in terms of trying to sort out, is it
        chasing after something that's going to show significance,
        or is it something that you really believe is the best
        method.
                 The other point that really bothers me is that
        I can't sort out what the primary variables are.  It seems
        to me like there are a lot of primary variables, which
        means that there is a lot of testing that is going to go
        on.  And now it looks like there is only a couple of
        primary variables, which means maybe there shouldn't be too
        much adjusting.
                 Could someone really clarify?  I thought I
        heard a presentation that there were a lot of secondary
        variables, but in the materials I had, there were something
        like six primary variables.  That would lead you to say
        that you committed to those variables.
                 DR. COHN:  The protocol did have, I think, six
        variables as primary endpoints.  I know if I were rewriting
        the protocol today -- and I can't do that -- and we had in
        mind a regulatory consideration, we would have more
        precisely defined what were primary and what were
        secondary.  In 1979, that was not done.
                 We all knew as we were progressing -- and we
        certainly have learned since then -- that the important
        variables are the ones that I focused on this morning
        because we now know those are the important variables in
        heart failure.
                 How did we learn that?  We learned that from
        V-HeFT.  So, this is a self-fulfilling prophecy.  You do
        the study, you learn about the disease by doing the study,
        and then it would be nice to then go back and redesign your
        protocol, but we don't have the luxury to do that.
                 So, what you are saying is correct.  One has to
        recognize there were a number of variables.  
                 The beauty, of course, of this is that every
        variable went in the same direction.  So, we haven't hidden
        anything.  I have alluded to some of those.  The trends
        were all favorable in everything that we looked at.  I hope
        that gives some comfort to the agency in the approval of
        the drug because there really is consistency across all the
        variables.
                 DR. D'AGOSTINO:  One of the concerns that I
        think we might have with that is that you then really use
        the study in an exploratory fashion, which is we learn from
        studies.  But it still then leaves us with the sense that,
        do we believe the way the variables ultimately were sorted
        out would, in fact, be confirmed in yet another trial.  I
        think this is where my problems come from.
                 DR. COHN:  We have what we believe is strong
        support for the other variables in V-HeFT II.  So, you have
        seen two trials in which the second -- the other endpoints
        all went in the same direction, and I think that should
        give you confidence that V-HeFT I has been replicated.
                 DR. MASSIE:  JoAnn?
                 DR. LINDENFELD:  Dr. Cohn, I have some concerns
        about dosing intervals.  V-HeFT I and V-HeFT II were both
        q.i.d., and I understand the approval is for t.i.d., or is
        it for q.i.d.?
                 DR. COHN:  No, the approval should be for
        q.i.d.  The data are q.i.d.
                 DR. LINDENFELD:  All right, good.
                 DR. COHN:  I think some of the recommendations,
        at least in one of the guidelines, is for t.i.d., based
        upon intuition, certainly not based upon data, and we are
        here with data, not intuition.
                 DR. LINDENFELD:  Good.
                 DR. MASSIE:  I'm just going to go to our
        consultants first and then we will open it up to the whole
        committee.  Bob and Jim, any comments, questions?
                 DR. CODY:  A couple of questions.  Did any
        patients who participated in V-HeFT I participate in V-HeFT
        II?  How many would you say, what percentage?
                 DR. COHN:  Yes.  I think about 15 to 20 percent
        of V-HeFT I patients who survived V-HeFT I were recycled
        and re-randomized into V-HeFT II.  This of course is a
        major reason why we have never merged these two databases
        because of the overlap of patients.  
                 We have done extensive analysis to see whether
        there was any difference in behavior of those patients who
        were re-randomized as compared to those new patients
        entered into V-HeFT II, and there appeared to be no
        interaction whatsoever.  So, we feel comfortable that they
        can be treated as if they were the same subset -- from the
        same set of the population, but that does influence a
        couple of things in terms of age, for instance.  They
        already were a few years older.
                 DR. CODY:  In terms of the very sophisticated
        statistical analyses that have been done and presented
        today, has this been factored in, or does it need to be
        factored in?  I would have to defer that to people who know
        a lot more about statistics than I do.
                 DR. QUINN:  Actually I can answer that
        question, that the results were done both ways for V-HeFT
        II, both using all the patients that were randomized to
        that trial, as well as looking at the patients that had not
        been in the V-HeFT I study.  The results were absolutely
        consistent using both methods.
                 DR. CODY:  What percentage of the patients in
        V-HeFT I and II were women?
                 DR. QUINN:  There were no women in the trial. 
        It was all conducted in the VA hospital setting.
                 DR. CODY:  I raise this because of the current
        VA and NIH push to include women in heart failure trials in
        a more representative fashion.  This is certainly an issue
        with at least one of the VA-sponsored heart failure trials
        that are currently underway.  
                 We are assuming that we could extrapolate these
        findings across genders.  Is that a reasonable assumption?
                 DR. COHN:  Well, I guess your assumption, Jeff,
        is as good as mine.  Certainly when one has looked at the
        response in women versus men in the trials where both
        groups have been included, such as the SOLVD trial, there
        appeared to be no difference in the therapeutic response.
                 Women were not included in V-HeFT because we
        recognized we would have so few that it would not be
        possible to analyze them separately, so we confined the
        study to males.  The extrapolation to the female population
        then is going to be a matter of judgment rather than of
        data.
                 DR. CODY:  I guess a final comment is, I think
        a very important statement that has been made by the
        presenters, and that is the need for prescribing
        information for this combination.  What data exists to
        suggest or to guide people when to use BiDil instead of an
        ACE inhibitor?  When do you use BiDil in addition to an ACE
        inhibitor, and can these findings of functional class 2 and
        3 patients be extrapolated to functional class 4.
                 DR. COHN:  Your last comment is a very
        important one, and since there was an exercise entrance
        criteria in all of these patients, class 4 patients were
        substantially eliminated from the trial.  There were a
        smattering of patients who were said to be in class 4
        failure, and as you know, a patient might have been in
        class 4 failure last month and now is ambulatory and
        functional and gets included in the trial.  Is he now a
        class 4 or is he a class 3?  We argue about that all the
        time.
                 But there really is little data in class 4
        patients in this trial.  There is a good deal of experience
        with the combination therapy clinically on hemodynamics in
        class 4 failure, but they were not included in this trial.
                 I think your first issue was --
                 DR. CODY:  Using BiDil instead of an ACE
        inhibitor or in addition to?
                 DR. COHN:  Yes, the place of this in therapy. 
        Obviously, the labeling that is being requested would point
        this out as alternative therapy to an ACE inhibitor in
        patients who were not receiving an ACE inhibitor usually
        because of intolerance or perceived intolerance.  We know
        that the analyses done of the use of ACE inhibitors in
        patients with heart failure continues to suggest that there
        is a large number of patients not receiving an ACE
        inhibitor who, on the basis of the data, should be
        receiving an ACE inhibitor.  So, this would be alternative
        therapy for that group of patients who physicians choose
        not to use an ACE inhibitor.  
                 We are providing no data on this combination
        added to an ACE inhibitor, and we would not anticipate that
        that should be included in the labeling.  Many of us in
        clinical practice use that combination because we have
        found anecdotally that it is effective.  But there have
        been no systematic studies done of hydralazine-isosorbide
        dinitrate added to an ACE inhibitor to justify that as a
        labeling indication.
                 DR. CODY:  I agree with you that that there are
        patients where we would use the combination, and generally
        those would be the patients who aren't doing well.  They
        might be the functional class 4 patients who are not
        responding to an ACE inhibitor or the hydralazine nitrates,
        so we combine them.  Where clinically, where this piling on
        concept is used for the sickest patients, do we have to
        have some special wording or recommendations about that?
                 DR. COHN:  Yes, I agree with you completely,
        Bob.  That is really the way we have to focus this therapy
        based upon the data from V-HeFT.  We have to limit the
        indication to what has been demonstrated in V-HeFT.  I
        appreciate your comments, Bob.
                 DR. MASSIE:  Just one qualification and then
        Ray has a question.
                 When you say in people who are not using ACE
        inhibitors, would it make more sense in people who have
        been tried on ACE inhibitors and have not tolerated them? 
        In order to best serve the educational function that what
        we are trying to do is get people to use ACE inhibitors and
        we know there are people in whom you can't, but not just in
        people who are not on them because that would be any heart
        failure patient who is newly diagnosed and hasn't yet had a
        chance to be treated.
                 DR. COHN:  Well, you know, you may be right. 
        On the other hand, if you look at the ancillary endpoints
        such as exercise, and one had a therapeutic goal in an
        individual in whom prolongation of life, based on whatever
        other issues might be present in that individual, was not
        your primary emphasis, and your primary emphasis was to
        allow the patient to do a little more exercise, one might
        conceivably feel that in that instance the mortality
        benefit of Enalapril was not important to this patient.
                 Now, these are judgmental issues that
        physicians have to cope with, so it is difficult to demand
        that all physicians give all patients with heart failure an
        ACE inhibitor.  It is important to show them the benefit of
        ACE inhibitors so that they can choose to use those drugs
        in the appropriate patient population.  So, it is a very
        nebulous kind of distinction, but I think physicians have
        to be given choices.
                 DR. MASSIE:  Ray?
                 DR. LIPICKY:  I have forgotten the operant
        policy during the studies with respect to how the dose was
        manipulated with respect --
                 DR. MASSIE:  Can you speak a little louder,
        please?  
                 DR. LIPICKY:  Sorry.  I have forgotten the
        operant policy with respect to how dose was manipulated
        during the studies.  Was it titrate to maximum tolerated
        dose with some upper limit?
                 DR. COHN:  Yes.  The upper limit was 40
        milligrams 4 times a day of isosorbide dinitrate, and 75
        milligrams 4 times a day of hydralazine.  It was a dual
        titration, and that is, both drugs were increased at
        subsequent visits until the patient achieved that higher
        dose.  
                 If headache, which was the major side effect,
        intervened, the dose could be either held or even reduced,
        and that is why the mean dose in V-HeFT I was about 240
        milligrams of hydralazine, not 300, and the mean dose of
        isosorbide dinitrate was about 110 milligrams and not 160
        milligrams reflecting that.
                 DR. LIPICKY:  But dose was increased for both.
                 DR. COHN:  For both.
                 DR. LIPICKY:  They were not changed
        independently.
                 DR. COHN:  No.  Although if a side effect
        occurred, the physicians were encouraged to reduce the dose
        of the ISDN first because it was our impression that that
        was the more likely cause of headache.  So, they might have
        reduced one and not the other.  And sometimes they
        discontinued one and not the other.
                 Now, we had a little trouble dealing with that
        discontinuation of one of the drugs because they were
        taking one and they weren't taking two.  Knowing what we
        know now, it's possible you need to take both in order to
        get the beneficial effect.  But it was all an intent-to-treat analysis anyway, so that analysis was not influenced
        by whether they did or didn't take both drugs.
                 DR. LIPICKY:  From the vantage point of
        instructions for use, and based on the experience, do you
        think it's a problem that one has to take both and does not
        have a choice in titrating one or the other, depending on
        adverse symptoms?
                 DR. COHN:  I think our data would suggest that
        if one wants to attain the benefit of this drug
        combination, one should use the two drugs.  We have no way
        of analyzing what the optimal dose of each of those two
        combinations is, as you know, and this was not a dose
        response study.  So, we are left with a strategy for
        therapy, a strategy for reducing the dose if side effects
        occurred, and when one used that strategy, we reduce
        mortality.
                 Now, I think from a labeling standpoint, all we
        can do is recommend that strategy in the labeling, knowing
        full well that that may not be the optimal strategy or the
        only strategy, but the only strategy we studied.
                 DR. MASSIE:  Ray, while you have the
        microphone, before we open the general discussion, maybe we
        can get you to clarify something for us.  The idea of a
        combination drug as opposed to the two components of the
        drug.  I think you started hinting on that point a bit.
                 What would the FDA see as a reason for
        approving a combination drug when we have the two
        components, and I guess then I would like Jay to follow up
        and tell us why he thinks it is better to have this
        combination rather than the two components, what advantage
        it provides, because ordinarily I know in combination drugs
        where we have dealt with them for hypertension, you have to
        show both components are effective and then there is some
        advantage to having the two together.  Maybe, Ray, you
        could tell us why we should be thinking about this.
                 DR. LIPICKY:  It could be a very long
        discussion but I think the short discussion is that if one
        has a trial where one thinks there has been documentation
        of an alteration in irreversible harm, and one knew that,
        say, it was a single chemical entity, but it was a
        racemate, nobody would have any problems whatsoever in
        saying that the drug, a racemate, did it.
                 I think that if you consider this to have been
        documented, to have an effect on something that is
        irreversible, well, then you are stuck, or not stuck.  It
        is appropriate to consider the combination as a single
        drug.  
                 Ordinarily one would expect to be able to
        document that drug A plus drug B has a bigger effect than
        either drug A or drug B alone at the appropriate doses. 
        But ordinarily one would be concerned about that if one
        could in fact do studies that would allow one to determine
        that.  It is unlikely to be able to do them for
        irreversible harm, especially with a study that is 20 years
        old.
                 DR. TEMPLE:  Barry?
                 DR. MASSIE:  Can I just let Jay respond?
                 DR. TEMPLE:  Barry?  I'd like to add something.
                 DR. MASSIE:  Go ahead.
                 DR. TEMPLE:  We have a combination policy that
        doesn't distinguish really between taking the two drugs
        separately and putting them in the same tablet.  That is
        theoretically of no concern.  It is never a benefit to have
        them in one tablet except convenience.  There can't be a
        medical benefit from taking them together as both
        separately.  The question is, do they each contribute, as
        Ray said.  The longstanding policy is you have to
        demonstrate that each component makes a contribution. 
                 We have, however, tried to confront the
        question of, suppose somebody shows you that you've done
        something important with two drugs and it is really not
        possible anymore to test the two components because you
        can't have the placebo group to do it.
                 What we have said is, if there is a plausible
        basis for having both components, on theoretical grounds we
        would sort of live with the discomfort of approving the
        combination if it had an important effect on survival or
        irreversible morbidity or something like that.
                 DR. COHN:  I think the answer to your question,
        Barry, is a complicated one.  Let me put it this way. 
                 If one looks at the use of this drug
        combination in its generic form, out in the community,
        there is very little use of hydralazine.  There is
        substantial use of nitrates.  ISDN is widely employed in
        heart failure, without labeling, and without indication and
        without marketing.
                 Hydralazine is not used, perhaps for several
        reasons.  Number one, physicians don't like writing so many
        prescriptions because they would have to write two separate
        prescriptions.  Patients do not like taking so many pills. 
        And there is no dosage form available of hydralazine which
        matches the dosage form used in V-HeFT.  So, there are
        several impediments to the use of hydralazine.
                 The nitrate use suggests that physicians are
        very comfortable using ISDN because they are comfortable
        with that drug.  And they are using it for reasons which
        are mysterious because there is no existing database which
        suggests that ISDN should be used in patients with heart
        failure, other than the V-HeFT database, which we now
        believe strongly suggests, based upon the new data that I
        showed you, that hydralazine should be used along with
        ISDN.
                 So, having labeling for BiDil, if it will help
        physicians to understand the application, the dosing and
        the usefulness of these two drugs and can do it in a single
        prescription, with a single tablet that patients will be
        much more comfortable taking, I think it can have a
        profoundly favorable effect on the management of this
        syndrome because, despite the fact that all the guideline
        committees recommend using this combination, it is not
        being used. 
                 There has to be some explanation for that, and
        that's the best explanation I have, is what I have given
        you.
                 DR. MASSIE:  Okay.  Well, what we are going to
        do is, Jeff, since he has not gone, and then we will start
        from the right.
                 DR. BORER:  Most of the questions I had have
        been answered, but I need a clarification here, if I can
        have one, please, and then based on the response to that I
        have several questions I would like to pose.
                 First of all, I would like a clear statement of
        what is being requested for approval here.  What is the
        indication?  Are we talking about approving the combination
        for reducing mortality rate in patients with congestive
        heart failure, or are we being asked for approval of the
        combination for the treatment in general of people with
        heart failure because at least three things look like they
        get better, mortality rate and maybe exercise tolerance and
        maybe ejection fraction?
                 What indication is the sponsor seeking here in
        the approval process?
                 DR. COHN:  Well, I guess if you are speaking of
        the sponsor, maybe we should turn to the sponsor.  Cesare,
        do you want to respond to that as the sponsor?
                 DR. ORLANDI:  The indication that we are
        pursuing is for treatment of congestive heart failure in
        addition to digitalis and diuretics in patients actually
        not taking ACE inhibitors.  This is based, indeed, on data
        that we feel are convincing, that are mortality data and
        ejection fraction data.
                 DR. BORER:  Okay.  So, you are not specifically
        suggesting that the drug is indicated for reduction of
        mortality, but rather that it is indicated in general for
        treatment of patients with heart failure.  Is that right?
                 DR. ORLANDI:  We feel that we have demonstrated
        actually an effect on mortality as well.
                 DR. BORER:  I think that Jay is absolutely
        right, of course.  You can't be penalized for not doing
        what you didn't know to do at the time you did it because
        the data were not available.  I come to these data with a
        sort of a general bias in favor of the combination being
        good.
                 However, we are being asked to approve the
        combination for something here.  Now I understand that it
        is for the general treatment of patients with heart
        failure, particularly because of mortality reduction.  And
        that may be a good thing to do.
                 But if we are going to do that then obviously
        everybody has to feel comfortable with the consistency and
        reproducibility of the effects, and therefore there are a
        number of statistical considerations that I would like
        some, again, clarification about here.
                 I don't think that the p values are ironclad
        rules that one must follow because they say this or that,
        and I know the FDA regulations aren't written that way
        either.  They are guidelines.  
                 On the other hand, we have information really
        from two trials.  One of them was placebo-controlled.  As I
        look at the data, the general Gestalt is that ejection
        fraction clearly is improved when you give the combination. 
        That is a good thing.  Exercise tolerance, well, you know,
        it doesn't really quite make it statistically but it goes
        in the right way.  That is convincing.  And then we have
        mortality, which is of course a very compelling argument if
        it is a reasonable one.  
                 But that is where this desire I would have to
        be able to be convinced of the consistency and
        reproducibility of the results begins to founder a little
        bit because of statistical considerations that I am not
        sophisticated enough to really understand.
                 The way I see it, we have a hypothesis that
        allowed only a one-directional response, maybe reasonable,
        so we used a one-tailed t-test.  
                 We say that there is no penalty for looking at
        the data many times if you passed a predetermined boundary
        that was determined by the Data and Safety Monitoring
        Committee at an early look.  That may be right, but I have
        never heard that before, but maybe it is right.
                 We have multiple pre-specified endpoints and we
        have no penalty for looking at those, even though they
        presumably could have gone either way.  And that is okay
        because mortality is so important.  
                 But we only have one placebo-controlled trial
        and then we use a second trial where the placebo is present
        but it's a historical control.
                 So, all of that is not the way we are
        accustomed to seeing data, and I would like to have
        clarified for me whether it is really legitimate to say we
        don't have to pay a penalty after a pre-specified stopping
        rule is passed but we decide to go on anyway because we
        wanted to see if the result was consistent over time.
                 If it is really legitimate not to pay a penalty
        when we talk about consistency, if there are multiple pre-specified endpoints but there is one that really looks real
        good.  What's the answer to that?  Is there a statistician? 
        Lloyd, perhaps?
                 DR. MASSIE:  We've heard the answer from the
        sponsor.  I would like to have the answer from our two
        committee statisticians.
                 DR. COHN:  Could I just add one point here
        because I didn't bring this up before.  I am reading now
        from the V-HeFT I protocol under Sample Size and Duration. 
        "The primary objective of the study is to determine if the
        survival time is increased on vasodilator therapy as
        compared to the survival time in the placebo group."  That
        was the primary endpoint.  So, don't allow all these other
        endpoints to dilute that out.  It is the primary endpoint. 
                 DR. BORER:  That is a good point and I accept
        that.
                 DR. COHN:  I would like the response from the
        agency, but just to remind you, the reason for imposing a
        penalty for multiple looks is that you always have the
        opportunity to stop the trial if you surpass the guidelines
        for the endpoints and the multiple looks.
                 If you surpass the endpoint and don't stop the
        trial, you really have eliminated the need for any more
        penalty because you haven't responded to it in the first
        place.  So, the multiple looks have not really contributed
        to your final decision.  That is a nuance, and I would love
        to hear responses from the statisticians on that, but just
        intuitively it seems to me that makes sense.
                 DR. MASSIE:  Lem?
                 DR. MOYE:  I have somewhat a different view.
                 (Laughter.)  
                 DR. MOYE:  The purpose of corrections for
        multiple looks is to ensure that you have preserved the
        type 1 error at an acceptable bound.  The type 1 error, I
        think, is really a cause for lots of concern and lots of
        confusion.  
                 From my way of looking at it, the type 1 error
        is a matter of population protection.  The experimenters
        have an obligation to protect the population from which
        they derive their patients and the derived sample.  They
        protect the derived sample, of course, by taking care of
        the patients as best they can.  They protect the population
        by ensuring that they don't inflict unnecessary false
        positives or false negatives.
                 The way to provide the insurance for false
        positives is the alpha level.  For every decision that is
        made concerning a hypothesis test, you have the potential
        for sampling error propagation, and there are two ways to
        handle that.  The far superior way, again in my opinion, is
        for the investigators to handle it.  That is to say, the
        investigators must say with absolute clarity what they are
        going to do with the primary endpoint, how they are going
        to test it, and what they are going to do with secondary
        endpoints.  They must provide, if you will, a decision
        path, how they are going to work through the collection of
        endpoints that they have.  
                 They are in the best position to do it because
        they can do it prospectively.  They have an excellent fund
        of knowledge to do it, but I must confess they are not used
        to doing that, and perhaps the reason is that we have not
        asked them to do that.  Because we haven't, we find
        ourselves again in the position of trying to make some
        determination and some post hoc correction of these
        accumulated decisions.
                 I think if the investigators surrender their
        mandate, because that's what they have in the beginning,
        for controlling these alpha errors to us retrospectively,
        then it is up to us to come up with our own.  
                 My personal one is a very conservative one
        which penalizes investigators for each decision they make,
        so that in this circumstance that where the type 1 error at
        the 2-year interim analysis is very small, then you
        nevertheless accumulate some error because that decision
        may have been wrong.  You accumulate alpha from that and
        you move on, so that as one progresses through the
        secondary endpoints, the alpha eventually accumulates.  You
        stop when you reach the bound, whatever that bound happens
        to have been.  Typically it's at the .05 level.
                 So, I am arguing for, number one, for a
        prospective plan for the spending of alpha, but in its
        absence -- and most times I am afraid it is absent -- a
        very conservative post hoc plan for the accumulation of
        alpha, and that way we can ensure that the probability of
        making it at least a type 1 error from all of them is
        acceptably small for the population at large.
                 DR. MASSIE:  Ralph?
                 DR. D'AGOSTINO:  I agree very much with the
        spirit of what was just said, but I would like to add a
        couple of comments to it.  
                 I think this idea of saying you cross the
        boundary and then you no longer pay a penalty, well, as you
        cross the boundary you find later on that your mortality
        for the full study isn't significant.  Do you still believe
        it is significant because you crossed the boundary earlier?
                 Do you start running into making decisions
        later on that you will change your mind or you will do
        different things, depending on what those later analyses
        produce, and you have to have some kind of way of guiding
        yourself in terms of alpha -- I don't like this notion of
        alpha spending, but what do you believe about it as you
        start looking at the data in a further fashion?
                 I think that -- and this is a good example --
        you have marginal significance with the 2-year mortality. 
        I mean, why isn't it .001 so there was no confusion?  It is
        hovering around.  You fuss with one analysis and it crosses
        over the significance.  Another analysis and it becomes
        slightly better for you.  There is not a very comforted
        feeling on that, and these multiple looks at the data
        really can't be just dismissed as you have protected
        yourself earlier.
                 So, I think that we really are in a situation
        that we can't say you crossed the boundary, therefore you
        forget about the alpha.  I don't think that really is the
        case here.  
                 And I do think that this question that you
        raise -- and I was trying to say somewhat the same.  You
        come into this study with certain notions that you want to
        look at survival, and you've seen something that looks like
        a 2-year survival.  Will you see it again?  I am not sure
        you will see it again.  I am not sure I am convinced with
        what the data I have seen here.
                 And I realize that survival is the major thing,
        but you still carry with you six primary outcomes and what
        are you going to do with those?  Are you just going to
        ignore them?  Those are all sort of look-see.  I am not
        going to think about any significance on them?  You
        certainly are, and once you start playing that game, I
        think you have to say, how am I going to use my alpha, how
        am I going to be able to sit back and say, I really believe
        what I have.
                 And I think that we are left in a situation
        where we see the survival but I would like to see another
        test of it.
                 DR. MASSIE:  Jeff, do you have more?
                 DR. BORER:  No.
                 DR. MASSIE:  JoAnn, go ahead.
                 DR. LINDENDFELD:  Just in this same vein, I
        wonder when we use a second analysis to assess mortality,
        when we know that the first analysis has been borderline,
        does the second type of analysis need to be stricter than
        ordinary criteria, once we know that the initial analysis
        was of borderline significance?
                 DR. D'AGOSTINO:  Are you asking me that?
                 DR. LINDENDFELD:  Yes.
                 DR. D'AGOSTINO:  I'm not sure I know the
        question.  Are you saying if they put a second study
        together?
                 DR. LINDENFELD:  I'm sorry.  In the initial
        study, once you know the initial method of statistical
        analysis was of borderline significance, and we go to a
        second, already knowing that the first was borderline.
                 DR. MASSIE:  This is the log-rank versus the
        Cox?
                 DR. LINDENDFELD:  Versus the Cox, right. 
                 DR. D'AGOSTINO:  No.  This is the notion, I
        think, that was raised in the question, are you looking for
        the test that is going to do the best for you?
                 DR. LINDENFELD:  Exactly.  Shouldn't the second
        be perhaps stricter than if it was primary --
                 DR. D'AGOSTINO:  I think so and I think that
        there is real justification for that.  
                 Again, I don't see anything wrong with, say,
        doing an analysis that makes no adjustment for baseline
        variables, seeing where that goes, and then doing a sharper
        analysis that includes covariates to get rid of some of the
        variability.  I am not sure it's imbalances that you need
        to correct, but you want to reduce some of the variability.
                 But as you progress through that, if it is
        stated in the protocol that the real analysis that you are
        going to put your final weight on is the Cox regression
        that does all the covariates, then I think you can wait to
        see what that produces.  
                 But if your protocol says I am going to look at
        the log-rank and maybe look at the Cox, or it is unclear
        what you are going to do with the Cox, and then you really
        move to the Cox with the hope that it is going to give you
        some significance because the log-rank didn't, I think you
        are in a situation where you are beginning to doubt how
        much certainty you can get from the study.
                 DR. MASSIE:  I think the committee has been
        restive and also very cooperative in not interrupting.
                 We were scheduled for a break, but I would like
        to try to make a pass-through here and continue the
        discussion, starting down there.  Udho?
                 DR. THADANI:  I have a couple of comments and a
        couple of questions.  
                 I want to reiterate, the study of V-HeFT I and
        V-HeFT II was in class 2 and 3 failures, and only in
        females, so the application of what we say is only to those
        groups.  There is no data on top of ACE inhibitors from
        either of the trials.
                 Jay mentioned that the study started in 1980
        and since we did not know the moving target, it should not
        be penalized.  We learn with experience and the committee
        has to make a decision what we know now, not what was known
        before.  Life is a penalty.  As we get older, we are going
        to die sooner.  
                 Now, Jay mentioned that we don't know why
        nitrates are used without hydralazine, and I think about 30
        percent of the patients in CHF have coronary artery
        disease, in some studies 40 percent.  The reason nitrates
        alone are used are really for 20 percent despite --
        especially in class 2 and 3 failure, the angina.  So, we
        are using nitrates to treat angina, not necessarily heart
        failure symptoms.  It is difficult sometimes, when they are
        getting exercise-induced dyspnea, to distinguish how is
        heart failure versus how is angina.
                 So, I don't think I have much problem why we
        are not using hydralazine all the time in those patients. 
        That is a comment.
                 Jay, you mentioned in your very earlier
        statement that efficacy perhaps is not related to
        hemodynamics, and yet to turn around and you say, well,
        hydralazine probably prevents tolerance and probably is
        doing that, so it doesn't jibe.  
                 Now, one of the questions on tolerance with
        nitrates is a moving target.  We still don't know what
        exactly produces it.  That is why the sulfhydryl
        hypothesis, the neurohormones know the oxygen radical, and
        I could say there are receptors.  So, I really don't know
        what to call this.
                 Now, you are alluding to Dr. Elkayam's study
        that hydralazine prevented tolerance perhaps rebounding. 
        He is in the audience.  I am going to ask him again.  I
        have asked him several times before.  There is no
        hydralazine group in that study and the study was only 24
        hours.  So I have no clue whatsoever what it will do if you
        do it at 1 week or 2 weeks.  Perhaps it might delay the
        tolerance.  By 2 weeks there is no efficacy whatsoever.  
                 So, I am not willing to buy that as a data
        showing that -- postulation, yes, but not a convincing
        proof that that is how the combination is working.  So, I
        want a comment on that before I say something else. 
        Perhaps you or Uri, who is in the audience, want to allude
        to it.
                 DR. COHN:  Let me see if I can try to express
        the relationship between hemodynamics and long-term benefit
        because, yes, I did make the point that the hemodynamic
        effects that may well influence symptoms in the short term
        are not necessarily indicative of a long-term benefit.
                 Yes, it is true that nitrates on hemodynamics
        apparently produce tolerance.  Partial tolerance, we would
        say, because we have done some studies on nitrate therapy
        chronically and are able to demonstrate that, given with a
        drug-free interval at night, at 10 or 12 hours at night,
        that nitrate effect persists.
                 It is true that the benefit that Uri and Leung
        and others have shown with nitrate co-administration is on
        hemodynamics and is short-term.  So, it provides us a
        potential mechanism, but it certainly provides us no proof
        that the long-term benefit is enhanced by the combination
        and would not also occur with the individual drug.  I
        wouldn't suggest to you at all that these data can be
        directly extrapolated to the long-term effects of nitrates.
                 Now in our view, the long-term effects of
        nitrates on left ventricular remodeling are non-hemodynamic.  We have data in an animal preparation in the
        canine that when you administer nitrates for 3 months, you
        prevent the remodeling of the left ventricle without a
        demonstrable hemodynamic effect.  So, my view is that this
        mechanism of action of nitrates is through nitric oxide
        effect either on the interstitium and the collagen, or on
        the myocyte directly to alter the remodeling process.  I
        think there is growing support for the idea that this
        remodeling is a non-hemodynamic phenomenon.  
                 I have no idea whether tolerance develops at
        all to that effect.  We have no data that hydralazine would
        influence that effect whatsoever.  So like in most drugs --
        and I think this applies to practically every drug that has
        been approved by the FDA and that we use daily in practice
        -- we do not know how they work.  Much as we would love to
        know, we are always grasping at straws to try to find out
        how drugs such as ACE inhibitors work, or why do beta-blockers lower blood pressure.  I have no idea, but they
        do.  
                 So, we have to separate mechanism from efficacy
        to some extent.  We are dealing here with potential
        mechanisms, but clearly not proof of the mechanism of long-term efficacy.
                 DR. THADANI:  Also, I think I would like to
        point out that ISDN regimen uses four times, which angina
        is really no better than placebo in several studies.  So,
        it is a very different regimen.  So, I would like to
        suggest let's keep tolerance out of the discussion because
        you are talking about survival.  A combination may or may
        not be relevant.
                 Now, point two I want to make is that in the
        V-HeFT II, Enalapril was definitely superior to combination
        therapy with ISDN hydralazine.  There is no way about that,
        so that is a fact.  So, my judgment would be that even --
        which I use sometimes patients who do not tolerate the ACE,
        I would hate to suggest that we should put a broad labeling
        that patients should be -- this is an alternative
        treatment.  I think you have got a study in which you did a
        study and Enalapril came out ACE or better.
                 So, it's only in patients who are not able to
        tolerate ACE, not that they are not taking ACE because a
        lot of physicians do not prescribe ACE, or patients who
        have renal dysfunction, that might be the way to go.  
                 So, I think one has to be concerned when you
        are looking at the labeling issue.
                 The question was raised in the V-HeFT I.  You
        adjusted, depending on the headache, separately ISDN lower
        dose without leaving the hydralazine.  How are you going to
        do that with a combination?  Do you have any ideas, or what
        do you suggest we should be doing?
                 DR. MASSIE:  Just respond to that last question
        about the adjustment.
                 DR. COHN:  The combination has two different
        dosage forms which provide different relative amounts of
        ISDN and hydralazine.  So, there is some flexibility
        available by altering the tablet.
                 DR. MASSIE:  John, do you have a question?
                 DR. DiMARCO:  I am still a little bit
        uncomfortable about recommending a combination drug when we
        do not really have data about either of the agents.  Am I
        understanding you correctly, that you think that nitrates,
        appropriately administered with a drug-free interval, might
        produce the same effect you saw with the combination?
                 DR. COHN:  There is no data whatsoever on
        mortality or left ventricular remodeling.  All I am saying
        is that one can maintain the hemodynamic effect of nitrates
        if you administer them chronically in this patient
        population with heart failure, measuring hemodynamics.  But
        that has nothing to do with the long-term efficacy that we
        have demonstrated in this trial.  So, the answer is, we
        don't know.
                 DR. DiMARCO:  When you were planning the trial,
        why didn't you then have a nitrate control group?  Or a
        nitrate group?
                 DR. COHN:  This trial was done to prove
        concept.  This was vasodilator concept, and we wanted to
        use the most potent vasodilators we had available at that
        time to prove concept.  
                 You would never in 1997 design a mortality
        trial with 640 patients and three treatment arms.  Come on. 
        I mean, we are dealing with a different era.  We were
        breaking new ground.  We didn't know what the mortality was
        going to be.  We hit actually the placebo mortality right
        on.  That was really our predicted mortality, so we were
        remarkably fortunate in guessing right.  
                 But obviously the study is not powered the way
        one would power it today, and Dr. D'Agostino is indeed
        right.  Don't we wish we had a larger database from which
        we could then show a p value that no one would argue with?  
        Wouldn't we wish we had two trials that demonstrated
        efficacy against a placebo arm?
                 The latter is not possible because we can no
        longer do a placebo arm.  The former we have to live with
        what we have, and I urge you to remember that p values
        don't tell you much about the magnitude of effect, but they
        tell you something about the confidence you would have in
        that effect.
                 The magnitude of this effect is quite large. 
        The confidence is a little lower because it is a small
        study, and we have to temper our judgment based upon what
        we have, and not what we wish we had.
                 DR. MASSIE:  Before we cross to the left, Bob?
                 DR. TEMPLE:  It is tricky to watch all the
        dancing p values, but it seems to me one can summarize it
        by saying the results are analysis-dependent, and that if
        you make any kind of correction as suggested by Drs. Moye
        or D'Agostino, it is going to rise above nominal
        significance.  There could be an interminable debate about
        what that correction should be for the multiple endpoints,
        the multiple looks, and the fact that it was a three-group
        study.  For starters, you have got to correct for that.
                 So, in that sort of situation one wouldn't
        ordinarily say that the study is unusable, but one would
        then look to the next batch of data one has, and in
        particular look at V-HeFT II.  
                 I am interested in people's views about the
        novel, to say the least, approach to dealing with a study
        that actually showed inferiority of the drug in question to
        another therapy, which is not easy to do if you're an
        active drug, and relies on an imputed placebo group to
        conclude that even though it was inferior, it probably
        still had some effect and would have had some effect in a
        study of V-HeFT II size.
                 Now, that is a very novel argument, as I am
        sure Dr. Cohn knows, and given the unequivocally borderline
        at best values in the first study, what does one make of a
        confirmatory study that loses to Enalapril and has to beat
        a putative placebo that wasn't there?  How plausible is all
        that?  Because nobody is going to make V-HeFT I
        overwhelming.  There are too many things one can say about
        it.  So, it is crucial to know how to interpret V-HeFT II.
                 DR. COHN:  I would like to remind you, Bob,
        that although we all agree that Enalapril beat H/ISDN in
        V-HeFT II, it only did it at the 2-year time point, not
        overall.  And it was at the 2-year time point where there
        is much less argument about whether H/ISDN beat placebo. 
        It is the overall p value that we are worried about.
                 So, you can have it both ways.  If H/ISDN beat
        placebo at 2 years, then so did Enalapril beat H/ISDN.  If
        we look at the overall result, neither p value reaches the
        nominal level of significance, and we have to really look
        at these two studies then quite similarly.
                 DR. TEMPLE:  Jay, even the value at 2 years is
        not clear-cut.  Some of them are, depending on what you do,
        above .05, some are below .05, but that is completely
        uncorrected for things that need correcting.  At a minimum
        there is the Prazosin group.  You have got to make some
        correction for that.  
                 And I am not one for major corrections for
        multiple looks here, perhaps, but there were other
        endpoints and there were multiple analyses, and whatever
        you think the right correction is, it is borderline.  
                 Then at the 2-year time, which was the sort of
        agreed upon time, it actually lost to another drug.  So,
        you have to believe there is room for it to be somewhat
        effective but still not as effective as another drug in a
        study where the overall reduction in mortality was -- I
        don't know -- like 20 percent.  Sorry.  You didn't actually
        measure it.  It was likely to be in the neighborhood of 20
        or so percent based on other Enalapril data.  
                 That is a lot to believe.  I just wonder what
        people think about that.  
                 DR. MASSIE:  Let's move along to the left and
        see if any of the comments --
                 DR. LINDENFELD:  A quick question.  In terms of
        remodeling, in V-HeFT I there was echo data.  Was there a
        difference between the hydralazine-isodi group and placebo
        in terms of end diastolic dimension over time?
                 DR. COHN:  No, the data really were in concert. 
        That is, the LVIDD, I think, as we did it -- and we have
        improved our methodology since V-HeFT I, but the trends
        were the same.  Clearly, a less precise measurement than
        the MUGAs that we did sequentially, but the directional
        changes were the same.
                 DR. MOYE:  Just to respond to Bob's question,
        part of which I think was the notion of comparing to --
        having an imputed placebo group.  I confess to say that my
        reaction is over negative to that because to me it looks
        very much like a historical control.  There are differences
        in baseline characteristics between V-HeFT II and V-HeFT I
        and differences in the choice of medication.  I can't say
        that I have learned anything reliably from that kind of
        analysis approach.
                 DR. MASSIE:  I understand we are going to have
        a specific presentation relevant to that point by the
        division after the break.
                 DR. LIPICKY:  You have a specific question
        dealing with that point.  It would probably be good to have
        this discussion at the time that you are answering
        questions and not when you are trying to clarify the data.
                 DR. MASSIE:  Okay.  So, Bob, you've prepared us
        to get ready.
                 DR. WEBER:  Jay, I have got a couple of short
        questions.
                 First of all, you were talking earlier that
        many clinicians are reluctant to use hydralazine, or simply
        do not use hydralazine, for treating patients with
        congestive failure, and that may be partly because, in the
        minds of many physicians, hydralazine is not always an
        appropriate drug for patients who have got ischemic heart
        disease.
                 When you look back at the V-HeFT experiences,
        what proportion of patients in fact had that failure on the
        basis of ischemic disease, and was there any information
        whether the treatment was more effective in those with
        ischemic disease than those with other etiologies?
                 DR. COHN:  No.  As I pointed out, about 55
        percent of the patients in V-HeFT I had ischemic disease,
        as opposed to 45 percent non-ischemic.  The response was
        quite similar in the two groups.  We actually have a slide. 
        I don't think we want to waste our time showing it.  But
        the reduction in mortality in those with CAD and those
        without CAD was quite comparable.
                 DR. WEBER:  Beyond what you showed us -- and I
        must confess, I had not really been aware in depth of these
        data before -- that hydralazine may work to prevent the
        tolerance to the ISDN, do we have enough information to
        make a comment describing the clinical pharmacology of the
        product?
                 To me, if we are debating whether or not a
        combination is appropriate, is there some mechanism that we
        can reliably put down in writing that would provide
        encouragement and support for the use of the two drugs as a
        tandem?
                 DR. COHN:  You are talking about blood levels?
                 DR. WEBER:  If such were available.
                 DR. COHN:  Well, of course there are now a lot
        of data available because of the bioequivalence issue
        relating to the BiDil combination and the individual
        components.  If you want to get into that, I could ask some
        of those that have been directly involved with that to
        discuss it.
                 DR. LIPICKY:  Is that what you want?  Blood
        levels?
                 DR. WEBER:  No.  I am really looking more for a
        justification for the mechanism of the two drugs.
                 DR. LIPICKY:  How about death?  That is what
        Jay is offering us.  If you use them in combination, it
        saves lives.  Isn't that good enough?
                 DR. WEBER:  It certainly justifies the
        treatment.  I'm just coming back to --
                 DR. COHN:  Well, the pharmacologic mechanism
        that really led Joe Franciosa and I to use this combination
        was that when one gave isosorbide dinitrate by itself, the
        pulmonary capillary wedge pressure fell, and the cardiac
        output went up only a little bit. 
                 When one gave hydralazine alone, the pulmonary
        capillary wedge pressure barely changed, but the cardiac
        output went out a lot.  
                 When we gave the two together, we got a greater
        fall in pulmonary/capillary wedge pressure and a greater
        increase in cardiac output.  
                 So, hemodynamically these two drugs are indeed
        remarkably additive.
                 Now, you have got to put all that aside and
        say, that was a wonderful idea in 1978 or 1979, but now we
        understand the mechanism of long-term efficacy in heart
        failure is not related to that remarkable hemodynamic
        effect probably and relates to some other action of these
        two drugs together which favorably affect all these outcome
        measurements in heart failure.  And do we know exactly what
        they are?  I think I know, but I am in a minority and I
        haven't convinced everybody.
                 DR. WEBER:  One last quick question, and it is
        one that a couple of other people have already alluded to,
        but I think it is somewhat troubling.  
                 The labeling that was initially proposed was
        that BiDil would be used as an adjunct to diuretic and dig. 
        You then suggested -- your own phraseology was -- that it
        would be used as an alternative to an ACE inhibitor.  Those
        are slightly different.  I don't know if both can be
        reconciled into one instruction.  
                 But bearing in mind the thought that came up
        and hasn't really been talked about yet, the possibility of
        a mortality claim, and if that were the case, would the
        same labeling be in place, or would it just be a general
        mortality claim that might infer that the drug could be
        used in patients already receiving an ACE inhibitor?
                 Obviously, we don't have those data, but
        clearly we have to try and understand how in the real world
        physicians would interpret these labels.  What are we going
        to say?
                 DR. COHN:  Well, as you know, I am a strong
        advocate of ACE inhibitors to treat heart failure, and I
        believe any labeling for this drug combination would have
        to make it clear that ACE inhibitors produce a more
        favorable effect on mortality and should be employed as the
        agent of choice in patients with heart failure, and that
        this would be an alternative for those patients who, for
        one reason or another, are not using an ACE inhibitor, and
        that would usually be because of perceived intolerance to
        the drugs.  The instructions for use, then, need to be
        provided to physicians.  
                 But I think the labeling would have to make it
        abundantly clear that there is a mortality benefit from an
        ACE inhibitor as compared to this combination.
                 DR. MASSIE:  Cynthia?  Ray?
                 DR. LIPICKY:  I think that it might be useful
        to say that the exact labeling is something that may get
        worked out.  The thing that is at stake here is whether it
        should be approved, so that labeling would have to be
        written.  
                 DR. RODEN:  (Inaudible.)
                 DR. LIPICKY:  Well, I understand that.  If you
        are having trouble deciding whether it has an effect that
        trials have shown in patients with heart failure, then you
        are going to have to say it should not be approved.  If you
        are not having trouble in deciding what it does in patients
        with heart failure, you will be able to tell us how it
        should be labeled.
                 DR. WEBER:  No, I have no trouble deciding that
        it does something, Ray, I just want to know what it is.
                 (Laughter.)
                 DR. MASSIE:  Cynthia?
                 DR. RAEHL:  Dr. Cohn, in your experience, would
        you suggest that the most commonly prescribed of these
        products would be the two dosages with the 20 milligram
        ISDN component, based upon what you know was the maximum
        expected dose in the V-HeFT trials, and what was the actual
        mean ISDN dose in the range?
                 DR. COHN:  Well, I am not sure I could project
        what dose is going to be used.  Physicians tend to use
        drugs in lower doses than are recommended.  It's been our
        experience with ACE inhibitors that if you tell a physician
        to use an ACE inhibitor, he or she will use 2.5 milligrams
        of Enalapril once a day and feel that they have
        accomplished the therapeutic goal.  So, I can't predict
        which one is going to be used.
                 DR. RAEHL:  Well, the reason why I ask -- and
        perhaps it will come up in the biopharm review, but I would
        be interested in the prospective comments of the sponsor --
        is that assuming that many patients will not tolerate 160
        milligrams of ISDN a day, which I think is a good
        assumption, then the two middle doses of 37.5 and 20, and
        75 and 20 could come into play more often.
                 Yet, it appears to me from the biopharm review,
        we don't have what I would consider the very basic
        bioequivalency or dissolution data.  I must admit, I am
        quite surprised to see that at this stage of the
        investigative process.
                 DR. MASSIE:  Maybe a focused response on the
        biopharmacology.  Do we have a reasonable 20 milligram
        component of the nitrates in those pills?
                 DR. ORLANDI:  I would probably defer the
        question to Dr. Forrest who actually performed the studies.
                 DR. MASSIE:  You have to come up if you are
        going to comment.
                 DR. RAEHL:  I think to expedite this rather
        simple yes or no question, whether or not some of that
        basic bioequivalency data is available for those middle
        dosages.  Or maybe someone from the agency can give a quick
        answer.
                 DR. LIPICKY:  Yes, I should be able to but I
        can't.
                 DR. MASSIE:  I think the question is -- and I
        think this question is triggered by some concerns in the
        reviews by the agency, so maybe they can comment -- do we
        expect to get the same effect from this 20 milligram
        nitrate component of this pill as they have gotten from
        isosorbide dinitrate 20 milligrams?
                 DR. LIPICKY:  Well, maybe I can address that,
        and if I say something wrong, holler at me.  I am talking
        to the people who know the data, okay?  Because I am
        recalling it.
                 In the bioequivalence studies, where there was
        plasma concentration versus time, not in vitro dissolution
        now, but bioequivalence studies, the to-be-marketed
        formulation that was studied -- and was it one or two
        doses?  
                 VOICE:  Two doses.
                 DR. LIPICKY:  Two doses?  Low and high?  Fine. 
        The lowest dosage form and the highest dosage form, which
        is usually what we ask people to do, were not bioequivalent
        to anything.  They were not bioequivalent to ISDN as it is
        available on the market, or hydralazine as it is available
        on the market, or to either of the formulations that were
        in either V-HeFT I or V-HeFT II.
                 So, now when I have made such a broad, sweeping
        statement, what does that mean?  It means that the usual
        generic rule did not apply.  It was 21 percent, but it
        covered a whole range of dosing from 20 to 160 milligrams a
        day.  So, it is still titratable, it still covers plasma
        concentration ranges that probably one would achieve.  But
        in fact, it is not precisely bioequivalent, so it could
        never be a generic.  
                 So, from my vantage point, I don't think that's
        a big problem.  Since the instructions for use are titrate
        to maximum tolerated dose -- it isn't, give this dose and
        then sit back and wait.  It is, if that dose doesn't make
        people say they are sick, give them some more, and if that
        next dose doesn't make them sick, give them some more, and
        then they will have a mortality benefit.
                 So, it is titratable.  It is dose-proportional,
        but in fact it is not a generic product.  
                 Does that respond to your question or your
        concern?
                 DR. RAEHL:  I think it does, but it also raises
        the issue once again that even though instructions for many
        of these are to titrate to maximum tolerable dose, we know
        we don't do that.  That's medical practice.
                 DR. MASSIE:  Okay, we are going to try to take
        a break in about three or four minutes.  Let's just get the
        last two committee members' questions.
                 DR. KONSTAM:  I just had a comment and a
        question.  The comment relates to guidelines because with
        regard to our construct of the guideline with the Agency
        for Health Care Policy and Research, we grappled a lot with
        this issue of making recommendations for non-approved
        products.  I think Barry served on that committee, too.
                 I don't think it was the intention of our panel
        to usurp the role of the agency.  I think that we came to
        recognize that the criteria that we would use to make
        recommendations were of a different standard than
        regulatory standard.  They were sort of a clinician's
        surrogate, perhaps, I might call it, if you will.  I think
        we were concerned about safety and we were concerned that
        some medium level of evidence -- and there were a variety
        of different levels of evidence that we could use, but
        would accept therapies that were clearly short of a
        regulatory standard.
                 Now, having said that, if you are interested in
        getting people to follow a guideline, I agree with what Jay
        said, that the current preparations of these agents I think
        represent really very real practical obstacles to following
        those recommendations that would be overcome by the type of
        preparation that's under proposal, that is, if it can be
        found to meet the regulatory standard.  So just to say
        that.
                 The question I had relates to stopping the
        trial, or not stopping the trial.  I just wonder, why
        didn't you stop the trial after the fourth look?  You're
        saying at the end that you felt that it was unethical to do
        another placebo trial because you were convinced of the
        effect, but why weren't you convinced enough of that after
        the fourth look?
                 DR. COHN:  Well, that is actually a very
        difficult question and I have grappled with that recently
        in the light of new concepts that should we have stopped
        the trial.  I think Joe provided a list of the various
        reasons why the committee in the documents at that time
        listed why they were not stopping the trial, and obviously
        it was to learn more about the therapies, learn more about
        heart failure, learn more about the potential predictors of
        a favorable response, and to see whether the effect was
        durable, that is, did it last longer or was this going to
        be short-term.
                 I think it would have been an appropriate
        strategy at that point actually, in retrospect, to have
        stopped randomization for ethical reasons and to continue
        follow-up, which is an intermediate strategy that has been
        used in some trials to date.  
                 But at that time in 1983, we had no experience
        in this syndrome, and I was a strong advocate for
        continuing the trial because it was an important study.  I
        didn't think that the data at that point would be
        persuasive enough to let everyone in the world be treated
        with a combination, and therefore we needed to augment our
        database to learn more about the disease.  And we did.
                 But I think you are raising a very interesting
        ethical dilemma that the committee probably didn't spend as
        much time agonizing over as they should have.
                 DR. MASSIE:  Dan?
                 DR. RODEN:  I will take the opportunity to make
        one comment and then ask a couple of questions.  The
        comment echoes what Bob said, and that is, I am troubled by
        being asked to approve a compound or a preparation for
        which the indication is not very clear to me, and which is
        demonstrably inferior to currently available therapies,
        although I understand why we're here.
                 So my questions.  I have two.  One is the
        question of not mortality but of symptom relief.  You
        showed us some data showing improvement in ejection
        fraction, improvement in VO2, and I wonder if you can make
        some comment as to the sort of clinical significance of
        those as opposed to the statistical significance of those. 
        The changes seem to me pretty small.  So, that was one
        question.
                 Then the other question has to do with numbers
        of patients that were excluded from V-HeFT I on the way in. 
        This was touched on earlier with respect to the question of
        unstable angina, for example, and the reluctance to use
        hydralazine.  I can read the exclusion criteria but it
        doesn't really say how many patients were actually excluded
        from the trials on the way in for those kinds of reasons.
                 DR. COHN:  Yes.  I think there were 3,400
        patients screened and 640 entered.  So, it is about a 5 to
        1 ratio of screened to entered, if that's what you mean.
                 The reasons for exclusion were down that whole
        list, of course, and some of them were inability to perform
        an exercise test or chest pain during an exercise test that
        excluded them.  So, this is a selected population of
        patients in whom heart failure is causing their symptoms,
        not some other abnormality of their circulatory system.  
                 I think the issue about what the endpoint is is
        a very important one.  From my last or next-to-last slide,
        I look forward to the day when we will target therapies for
        specific mechanisms of disease or surrogates for disease,
        rather than for the disease in general because we throw
        people into convenient wastebaskets and call this a
        disease.
                 The labeling for this drug has been proposed to
        you for heart failure, and we know that heart failure is a
        heterogeneous syndrome with many different endpoints.  
                 DR. MASSIE:  Jay, can you make it specific? 
        Ejection fraction, exercise tolerance?
                 DR. COHN:  Yes.  
                 Now, you asked about peak VO2.  There is no way
        of defining clinically whether a statistical improvement in
        peak VO2 is really an endpoint that is important or only
        statistical.  As I showed you in V-HeFT II, H/ISDN would
        have been approved on the basis of exercise performance,
        statistically significant differences at 3 and 6 months,
        had this been a 6-month trial.
                 DR. RODEN:  You showed us VO2 data.  How about
        exercise time?
                 DR. COHN:  Well, VO2 was the primary endpoint
        defined in the protocol.  We have exercise time which
        follows the same path, but it was VO2 that was really
        chosen to be the exercise.  
                 Now, what we've learned, of course, and what
        was obviously intuitively apparent to everybody before was
        that when you do a long-term trial and look at non-mortality endpoints, you get a biased population
        progressively as the mortality difference enlarges.  So,
        data after 6 months is contaminated by the fact that people
        are dying and dropping out, and yet you are only studying
        the exercise in the survivors.  
                 And you can put a substitute in, but we didn't
        do that.  We have done that.  When you substitute for
        mortality, and give a low value of exercise to those people
        who died, which has been done in some trials, you obviously
        show a benefit of H/ISDN because the people are not dying. 
        And you get a very low value for the placebo group because
        they have died.  
                 So, that to me is not any longer looking at
        exercise.  That is looking at kind of an overall phenomenon
        which I find contaminated.  But that is another endpoint
        and it could have been used.
                 DR. MASSIE:  Just one quick question on my
        part.  It is interesting, if we look at resting VO2, it
        sometimes goes up during therapies, particularly
        sympathetically activating therapy.  These differences in
        peak VO2 were small enough that they potentially could be
        explained by a difference in the baseline pre-exercise VO2.
                 Did you do any statistics or analyses on the
        VO2 before exercise?
                 DR. COHN:  I can't recall that we did.  I think
        there was no significant change, but I can't recall if we
        really analyzed that, Barry.
                 DR. MASSIE:  I think it is an important issue
        because although you said directionally the exercise time
        went in a different direction -- I mean, went in the same
        direction, the statistics weren't there, and it was, as far
        as I remember, not even really close to significant at any
        point in time.
                 DR. COHN:  Well, the trouble with an exercise
        time measure is you have got flat workloads.  You can
        increase by 2 minutes and have the same workload, so that
        creates --
                 DR. MASSIE:  Peak VO2 should be better.  I just
        had that concern because certainly with some of the
        positive inotropes, I have seen an increase in resting VO2
        that is equal to the magnitude of the increase in peak VO2
        that we have seen there.
                 DR. THADANI:  One second before you finish that
        up.  
                 Looking at the graphs and the table on VO2 and
        exercise, VO2 again is a moving target, only showing
        benefit at 12 months, not other time points, and there is
        no significance at all on total exercise duration at any
        time points.
                 DR. MASSIE:  Correct.
                 DR. THADANI:  So, I think what is important. 
        Before we jump onto whether that is definitely beneficial,
        I have not seen any benefit.
                 DR. MASSIE:  Let's take a 15-minute break, and
        when we come back, it will be time for people from the
        agency to make any comments and then we'll go on to the
        questions.
                 (Recess.)
                 DR. MASSIE:  Before we move on to the
        questions, I do not know if there are any specific comments
        from the division reviewers that we haven't covered.  If
        there are, this would be a good time to raise any comments
        and questions.
                 DR. LIPICKY:  No, there are not.
                 DR. MASSIE:  There are not.  Okay.  So we
        thought of everything.
                 Well, I think, then, we should move on to the
        questions.  Maybe as we go through the preamble the rest of
        the committee will find their place.  I am not going to
        read the whole preamble which basically outlines what we
        are being asked to consider, the approval of BiDil, and
        some concerns related to multiplicity, bioequivalence,
        which I guess we have covered, and tolerance, which we have
        at least discussed.
                 The first set of questions starts with V-HeFT
        I, and I will read that in full because I think this is
        important.
                 Factors that might affect interpretation of the
        mortality results include the following.  
                 There were four interim analyses conducted by
        O'Brien/Fleming rules.  
                 The protocol outlined three possible
        comparisons in the primary analysis, using the log-rank
        test.  These comparisons included each active treatment arm
        to each other, the combined vasodilator arms to placebo,
        each active arm to placebo.  Each of these analyses was
        performed at least once during the course of the study.
                 There were two other analyses:  one, a protocol
        specified Cox regression intended to identify covariates
        that were important and, two, a retrospective Cox
        regression analysis for the placebo versus isosorbide
        dinitrate comparison, using baseline covariates specified
        by the division.  The Cox regression analysis required the
        somewhat arbitrary imputation of missing baseline values.
                 Mortality was specified to be evaluated as
        either total mortality over the duration of the study, or
        as the 2-year mortality, or at the 2-year point.
                 The published description of the study in the
        NDA submission reported nominal p values.  In interpreting
        the p values for mortality analyses in V-HeFT I, by what
        factor, if any, should the nominal p value be inflated for?
                 Now, some of these points we have touched on
        but I think we will revisit them briefly here.  My plan is
        to ask our statistical primary reviewer and consultant to
        comment first on the statistically related questions, and
        our clinical reviewer to comment first on the clinical, if
        I can make that distinction.  It is not always so easy.
                 So, I think this first one we will start from
        the statistical point of view.  Lem, multiple endpoints?
                 DR. MOYE:  I think I can answer questions 1.1
        through 1.5 very succinctly.  
                 First, I would say that the primary
        responsibility for setting corrections for endpoints in
        interim analysis reside with the investigators.  I think I
        mentioned that before.  I will just say briefly now.  If
        they don't do it, the responsibility devolves on us.
                 The spending function that I used allocates
        alpha as the instigators said they would for the primary
        endpoint.  Now, the primary endpoint alpha here is either
        .09 for a two-tailed test or about .046, I think, for the
        one-tailed test.  That already exceeds the type 1 error for
        the primary endpoint.
                 Any adjustments that I make to look at
        additional endpoints, be they primary or secondary
        endpoints, or times of treatments are going to increase the
        p values well above an acceptable level.  
                 So, I would say that the information that we
        get from the secondary endpoints here really is not
        contributory to making this study positive.  Now, you do
        learn a great deal from these analyses and from these
        evaluations, but it really doesn't add in an important way
        to making the study positive.
                 DR. MASSIE:  Let me just clarify that.  In
        making that statement you are not paying attention to the
        Cox proportional hazards model of what was stated to be the
        primary endpoint.  Is that correct?
                 DR. MOYE:  Right.  I was going to hold off on
        that until we got the question 3.  
                 Let me say briefly about that.  My read of the
        protocol is that the analysis plan was to be the log-rank,
        and to be in a position now where the log-rank says one
        thing and the Cox regression analysis says something else
        is pretty intolerable.
                 When I look to get out of that, I look first to
        see what the investigators said they were going to do.  My
        read of the protocol is that the investigators planned to
        put most of their weight prospectively on the log-rank.
                 Any other view of that, I think, runs very
        close to being a post hoc view because we now know what the
        data show and we now are in a position of having to choose
        our statistical analysis in view of the data we have before
        us.
                 The clearest and cleanest answer, I think, is
        to go with the log-rank.
                 DR. MASSIE:  And then let me, just being the
        devil's advocate, or I don't know what advocate, say, what
        about the fact the 2-year endpoint log-rank, I think, came
        much closer than the .09 to achieving statistical
        significance, at least nominally?  Wasn't that the case? 
        What was the log-rank p value?
                 DR. ORLANDI:  It was .056.
                 DR. MASSIE:  And that is for the two-tailed?
                 DR. COHN:  The one-tailed 2-year log-rank was
        what?  We will get that.
                 DR. MASSIE:  I guess of the hierarchy of
        endpoints, mortality was clearly meant to be the first one. 
        My reading, by the way, is that overall mortality was
        really clear --
                 DR. COHN:  The 2-year one-sided p-value log-rank, which was defined in the original proposal, was
        .0279.  There it is:  2-year mortality log-rank .0279. 
        With the Cox model it was .0168.
                 DR. MASSIE:  So again, I guess by Lem's
        criteria that wouldn't affect your answer to these
        questions either?
                 DR. MOYE:  That's correct.
                 DR. LIPICKY:  I am not sure that I understood
        Lem's answer.  May I ask you to clarify it so I understand?
                 DR. MOYE:  To which part?
                 DR. LIPICKY:  Well, to any part. 
                 (Laughter.)
                 DR. MOYE:  Okay.  
                 DR. LIPICKY:  Let's take the log-rank of .0279. 
        That is the nominal value.  Right?
                 DR. MOYE:  I guess I would say arguably,
        because my view of the protocol was that it was overall
        mortality and not 2-year.
                 DR. LIPICKY:  That's fine.  
                 So, that number needs to be adjusted somehow,
        or does it?  That is what 1.1 through 1.5 are asking.  That
        is, if you looked at that number, that looks to me like it
        is significant, but we know that all of these other things
        were done in addition to doing that.  How should that
        influence how I look at that number?  
                 DR. MOYE:  My view, Ray, is that this number is
        not significant.
                 DR. LIPICKY:  Why is that?
                 DR. MOYE:  Because the one-sided p value
        threshold was .025.  That's my read.  So, this is not
        significant.  They have exceeded their alpha, and so any
        other decisions I make on any other endpoints are going to
        further inflate alpha and therefore --
                 DR. LIPICKY:  Fine.  Then could I pick another
        analysis where you would not be able to say that?
                 DR. MOYE:  You can do anything you like, Ray.
                 (Laughter.)
                 DR. LIPICKY:  So, let's forget that the log-rank did meet their prespecified endpoint, and let's pick
        the Cox model of .0168.  So, they didn't prespecify what
        they had to do.  Right?
                 DR. MOYE:  Okay.  So, now --
                 DR. LIPICKY:  So, let's assume that that was
        the only test that was going to be done.
                 DR. MOYE:  Hypothetically they said the Cox
        model was going to be it and they hit at .0177.  Okay?
                 DR. LIPICKY:  Yes.  That's fine.  We'll pick
        overall mortality, .0177.  And that was the prespecified
        one to do, but all these other analyses were done also.
                 DR. MOYE:  Yes.
                 DR. LIPICKY:  How should that .0177 be viewed? 
        That's what these questions were meant to get at, okay,
        because that looks like a pretty significant number to me.
                 DR. MOYE:  Right, and the adjustment I would
        make in the analysis path, going through these endpoints,
        would be as follows.  I would leave the .0177 untouched.  I
        wouldn't snatch defeat from the jaws of victory for the
        investigation.  I would leave the .0177.
                 That does leave me some alpha left to spend on
        secondary and tertiary --
                 DR. LIPICKY:  But I'm not even interested in
        secondary and tertiary.  
                 I guess what this question was oriented towards
        asking was whether any of these p values for the primary
        endpoint can be taken at their face value.  Am I making
        sense?  Because there were interim analyses, because there
        was more than one primary endpoint, because there was more
        than one analysis.
                 DR. MOYE:  Okay, I understand.
                 DR. LIPICKY:  So, that is what this question
        was meant to get at, not what your bottom line is.
                 DR. MOYE:  Let me handle the interim analyses
        question first.  Decisions are made to continue the trial
        at prespecified time periods during the trial's duration. 
        That's spending alpha.
                 The way these interim monitoring rules are
        constructed is that the alpha that you spend is very, very
        minute.  So, in the end, I don't have .025 to spend.  Maybe
        I have .023 to spend.  So, from that point of view, the
        .0177 I think still stands.  
                 DR. LIPICKY:  It might be .0179 now, though.
                 DR. MOYE:  Right.
                 DR. LIPICKY:  That's the sort of look that I
        would like you to give it.
                 DR. MOYE:  Now, the issue of having multiple
        primary endpoints is a little problematic because what is
        required is a prospective statement by the investigators on
        how they are going to allocate their .025.
                 Now, if they are planning to allocate .025 to
        each of them, using kind of a Bonferroni approximation of
        the overall alpha, the overall alpha exceeds the -- or is
        at the .05 level, which is unacceptable for a one-sided
        test.
                 So, the investigators would need to say at what
        level they are going to accept each of the tests.
                 DR. LIPICKY:  But they didn't.
                 DR. MOYE:  But they did not.
                 DR. LIPICKY:  So, you've got to set it.
                 DR. MOYE:  I beg pardon?
                 DR.  LIPICKY:  So, you have to set it.
                 DR. MOYE:  That's right.  And so what I would
        do would be to say, if I have .025 to spend on either of
        them, that would be for me the probability of making at
        least one mistake, say a mistake on primary endpoint 1, a
        mistake on primary endpoint 2, or a mistake on both.
                 I would also say that I want to apportion alpha
        equally between the two because I do not have any reason to
        spend it more on one than the other.  
                 DR. COHN:  They are very interrelated
        endpoints.  Aren't they?
                 DR. MOYE:  Well, we're going to get there. 
        Next point is I would also assume that they are
        independent.  Now, that is very conservative and I am doing
        it for two reasons.  Number one, because the investigators
        let me down and didn't do it up front.  And number two,
        because I don't know exactly what the nature of the
        dependency is.  It is easy to argue about the dependency
        but I would have to specify exactly what the nature of the
        dependency is.
                 DR. FISHER:  Can I ask a technical question?
                 DR. MOYE:  Yes, sir.
                 DR. FISHER:  If you perform a randomization
        test and take the minimum p value, you are absolutely
        protected by all of our rules and it takes into account the
        unknown correlational structure.  In other words, you let
        the data tell you, but because you are doing the
        randomization test, it strikes me when you have highly
        correlated endpoints, that makes much more sense to most
        statisticians, I would say, than to assume the worst case,
        or do a Bonferroni or whatever.
                 DR. MOYE:  Well, I guess I am just a little
        uncomfortable, and maybe most statisticians are not, but I
        am just a little uncomfortable with the randomization test. 
        I am much more comfortable with -- I am most comfortable,
        if I can say this, with the investigators saying exactly
        what they are going to do.  
                 Once they have not done that, then the
        floodgates open and we can all bring our different alpha
        spending functions to bear.  
                 If the question is how I would approach this, I
        would approach it as I said, and make conservative
        assumptions because, again, I want to be sure that I am
        preserving the type 1 error at a minimum bound, considering
        the issues that have come up today.
                 DR. MASSIE:  Let me interrupt.  We have a lot
        of questions and I don't want to get into a technical
        statistical thing.  I think what we're doing now is
        instructive, Ray, making Lem put his money where his mouth
        is, so to speak.
                 DR. MOYE:  Put my alpha where my mouth is.
                 DR. MASSIE:  And we should go through that
        quickly, and we have a second statistician we are going to
        bring up the same opinions on.  Let's stay away from
        philosophy and just hit the questions.
                 DR. MOYE:  So, Ray, I would work through the
        very small amount of algebra and I would come up with a
        number.
                 DR. LIPICKY:  Yes, well, can you give a guess
        as to what that would be?
                 DR. MOYE:  Sure.
                 DR. LIPICKY:  I guess what I am looking for is
        some limits here because what you are saying, as I
        understand it, is that because of whatever was done in the
        beginning, you are being given the latitude to make the
        rule anything you want to make it.  
                 DR. MOYE:  Yes.
                 DR. LIPICKY:  So what I am looking for is what
        that limit would be, and how .0177 fits into that.
                 DR. MOYE:  Right.  For two primary endpoints,
        let's say the overall alpha after the interim monitoring
        was .024.  Then I would come up with about .013.
                 DR. LIPICKY:  And that is just for two --
                 DR. MOYE:  For two primaries.
                 DR. LIPICKY:  For two primaries, and there were
        six.
                 DR. MOYE:  If there were six, it would be --      
                 DR. MASSIE:  Come on, Ray.  We know that they
        identified a single primary endpoint.
                 DR. LIPICKY:  No.
                 DR. MASSIE:  There were not six endpoints I
        think from the way the protocol was written.
                 DR. COHN:  The protocol was written that
        mortality is the major endpoint of the trial, and it links
        2-year and overall, which are closely correlated.  So, you
        don't spend all your alpha --
                 DR. LIPICKY:  Well, okay, let's be sure we
        understand exactly what's being said here.  There is no
        question that the trial was sized on the basis of
        mortality.
                 DR. COHN:  And the statement is in the
        statistical analysis that the primary endpoint is
        mortality.
                 DR. LIPICKY:  Right, but elsewhere in the
        protocol it says we have these primary outcomes.
                 DR. COHN:  It was probably not written
        properly.  They were all listed as primary endpoints but
        the primary endpoint was really the mortality.  The others
        should have been listed as secondary, and they weren't.
                 DR. LIPICKY:  Fine.
                 DR. COHN:  I plead guilty.
                 DR. LIPICKY:  Okay, so that's for that.  
                 And then for the multiple statistical methods,
        do you need make some other correction because the problem
        is we have all these analyses to look at and some of them
        look pretty good.
                 DR. MOYE:  Well, the correction I make really
        is one that frankly ignores the other analyses.  I  go
        exclusively by what the investigators said they were going
        to do.  I rely on their diligence and their efforts in
        putting together an acceptable protocol, and that means --
                 DR. LIPICKY:  Right, but I said that it was
        okay for them to do a Cox analysis.
                 DR. MOYE:  Yes.  I don't know why. 
                 (Laughter.)
                 DR. LIPICKY:  And so since I said it was okay,
        they did it and now I have another p value.  What am I
        going to do with that?
                 DR. MOYE:  My advice to you, sir, is to ignore
        it.
                 DR. MASSIE:  Let's just say that they made the
        point and said, they are both very important and if either
        one comes up positive, we are going to call it a positive
        trial.  Let's say they have written it that way because
        some might read it that way.
                 DR. MOYE:  Okay.  Well, if they had written it
        that way, then I would have them apportion alpha for each
        of those tests that they did.  Here I think I guess I would
        be a little more amenable to the point that Jay brought up
        about there being correlation here.  I am not sure I know
        exactly --
                 DR. LIPICKY:  Okay.  I think I understand what
        you are saying and I have it in perspective with respect to
        these two numbers and that is fine now, as far as I am
        concerned.  If Dr. D'Agostino might comment a little bit.
                 DR. MASSIE:  Let's take Lem off the hot seat
        and have Ralph comment on those five sort of statistical --
                 DR. D'AGOSTINO:  When I was dean of the
        graduate school at BU, the faculty would come in or the
        chairman would come in and you would expect from the
        sciences this rigorous evaluation of their faculty for
        salary increases, and you would expect maybe the people
        from humanities would be a little bit more loose about it.
                 Well, what used to happen is that the
        humanities would come in with these scales on how they
        rated their faculty and the mathematics used to come in and
        say, this guy is a good guy and so forth.
                 I am a statistician, but I am going to just say
        this is easy to handle because if I look at the best world
        that they produce in terms of their hypotheses testing, and
        you want to do lots of different tests and what have you,
        none of them are smashing.  The levels of significance are
        not marginal.  They are significant by our rules if this
        was the only thing they are looking at, but they have five
        or six endpoints to run around with.  They have three
        groups to deal with.
                 Multiply it anyway you please.  It really is
        that once you start saying that there are multiple
        activities going on here, all of these are levels of
        significance that they have quickly run you into seven,
        eight p's of .07 or .9 and so forth, or .09, .10.  They
        quickly get you beyond what we conventionally think.
                 I think that this is a nice study but there is
        so much going on that nothing comes out that clear that can
        really stand up to any kind of adjustments that you want to
        make.  
                 I am willing to let them do the Cox regression. 
        I am still not impressed by the final answer they get.
                 DR. MASSIE:  Is that good enough for you, or do
        you want to get specific answers?
                 DR. LIPICKY:  That discussion actually answers
        2 and 3 also.  So, you just got through three questions.
                 DR. D'AGOSTINO:  Thank you.
                 DR. MASSIE:  Maybe I should thank you too, but
        I think before we jump to 4, if anybody has some burning
        comments on the committee, let's hear that.
                 DR. TEMPLE:  You may well have answered all the
        questions, but the way this was formed was to see if you
        could put more specific numbers on at least some components
        of that, and maybe that's asking a question that's
        unreasonable and you have to resort to the Gestalt.
                 But, for example, having three groups is fairly
        specific, three groups with a common placebo.  You are
        going to hear another thing later in this meeting where
        someone said, well, my critical p value is therefore .035
        because I have three groups and the common placebo.  So, it
        is not quite Bonferroni because there is a shared placebo,
        so they are not independent.  That is one component of
        this, surely, that's easy to put a number on.  
                 So I guess my thinking was, whatever you say
        the value here is, you have got it inflate by 50 percent
        or --
                 DR. D'AGOSTINO:  Well, I am trying to say the
        same thing.  Because you have the three groups, there is
        this sort of multiplication right there.  Because you have
        a number of endpoints, there is a multiplication there. 
        There is no way that I can take this reading that they
        aren't declaring these as primary endpoints.
                 I know the primary primary is mortality, but
        the other ones are still called primary and I don't know
        what that means if it doesn't mean that they are the major
        variables.
                 DR. TEMPLE:  Of course, some of those sort of
        lean, and I have never understood how, if you have six
        endpoints and some of them are sort of marginal, you adjust
        your correction for that.  That's for another two-week
        workshop.
                 DR. MASSIE:  Udho.
                 DR. THADANI:  Barry, I think one of the things
        which disturbs me, if we stick to the protocol, that it not
        show a significant log-rank and then you could show how we
        can do different statistics to prove the point.  I think
        here we are making a decision on, as has been alluded by
        the two statisticians, that log-rank was negative and you
        could bring a lot of tests.  I think we have to live with
        what the data is, and so one has concerns.
                 DR. MASSIE:  Yes, I just think, because
        obviously there are some implications of skipping
        immediately to question 4 from this, that if you put it in
        the best light, the protocol did specify two different
        tests up front.  They did give some alpha, specifically for
        in fact the multiple comparisons, and they did talk about
        both 2-year and total mortality.
                 My own reaction is, you have to obviously
        adjust for the groups and if you are willing to let 2-year
        mortality rise to the level of total mortality -- and it
        seemed to me there really was a differential emphasis in
        the protocol -- then you really would have to correct in
        some way for that and nobody has told us exactly how
        because I don't think they are totally independent
        endpoints.  You would expect that they would track to some
        extent.
                 But we have heard our two statisticians tell us
        that whether they look at it in a quantitative way or in a
        qualitative way that they are not blown away by the
        certainty of this result.
                 DR. D'AGOSTINO:  Another point to mention here,
        which I think has been mentioned a couple of times, if
        there is no guidance in the protocol on how one divides
        this alpha up, then you can't take the attitude of using
        the sharpest way of doing it and taking into the
        correlation and so forth because then you are playing the
        same game the protocol has played.  There is nothing there.
                 If you are going to get to these numbers, you
        have to take a sort of conservative view.  There are three
        groups, so there's that multiplication.  There are six
        endpoints and there's that multiplication.  I don't see how
        you can get out of that.
                 DR. MASSIE:  Okay.  Are we ready to move on to
        question 4?  
                 Was there a statistically significant effect
        found in V-HeFT I for mortality in the entire study, first,
        and I guess in terms of discussion, 2-year mortality?  We
        might have comments on both of those.
                 Let me ask JoAnn her thoughts, having heard the
        statisticians' input.
                 DR. LINDENFELD:  Well, I think we have heard
        all of those and it is still very borderline in the best
        case, that mortality at 2 years or in the entire study
        period is significant.
                 DR. MASSIE:  Any other comments from the
        committee?
                 DR. THADANI:  Are you asking whether you are
        convinced or not?  Is that what you're saying?
                 DR. MASSIE:  Yes.  We are being asked whether
        there was a statistically significant effect, having
        considered what the level of significance might need to be
        for all of the questions raised in 1, and obviously one
        would have to, I guess, be persuaded by the Cox more than
        the log-rank if we were going to say yes.
                 DR. THADANI:  We are already implying that we
        are going to rely more on log-rank, and the answer has to
        be no, I am not convinced it has shown a benefit.
                 DR. LINDENFELD:  And this was discussed in
        earlier meetings and it was suggested that some
        confirmatory data would be needed to support this.  I guess
        we will go on and discuss that in a minute.  Because of the
        borderline significance.
                 DR. MASSIE:  You mean earlier FDA discussions
        with the sponsor?
                 DR. LINDENFELD:  Right, in earlier FDA
        discussions.
                 DR. MASSIE:  Any comments from the left?  It
        sounds like this is something we need to vote on.
                 DR.  LIPICKY:  Yes, please.
                 DR. MASSIE:  Okay.  Let's start down at the
        left-hand end of the table.  We are voting whether there
        was a statistically significant effect on mortality during
        the entire study period for V-HeFT I.  Dan, you want to
        lead off?
                 DR. RODEN:  No.
                 DR. KONSTAM:  Well, I always feel awkward
        voting on this sort of question because this is the sort of
        question I ask my statistician, and I haven't heard any of
        our statistical advisers advise us that the answer to this
        question is yes, so I don't see how I can vote anything
        other than no.
                 DR. RAEHL:  No.
                 DR. WEBER:  Now, this not the 2-year.  
                 DR. MASSIE:  No.  I think they are asked
        separately.
                 DR. WEBER:  In that case, for the moment, no.
                 DR. MOYE:  No for the overall.
                 DR. LINDENFELD:  No.
                 DR. MASSIE:  No.
                 DR. DiMARCO:  No.
                 DR. THADANI:  No.
                 DR. GRINES:  No.
                 DR. BORER:  No.
                 DR. D'AGOSTINO:  No.
                 DR. MASSIE:  Okay.  Well, I guess the same
        question, then.  Was there a statistically significant
        effect found in V-HeFT I for 2-year mortality?  I think it
        is only fair to start at the other end.  I don't know
        whether the other end starts with Ralph or Cindy.  We'll
        let Ralph go first.
                 DR. D'AGOSTINO:  Well, if we are consistent
        with the discussion we had in 1, 2, and 3, we have to say
        no.
                 DR. BORER:  I agree.  No.
                 DR. MASSIE:  Bob is not allowed to vote.
                 DR. GRINES:  No.
                 DR. THADANI:  No.
                 DR. DiMARCO:  No.
                 DR. MASSIE:  Well, I also will have to say no,
        since I have to rely on the statisticians to some extent.
                 DR. LINDENFELD:  No.
                 DR. MOYE:  No, for 2-year.
                 DR. WEBER:  No.
                 DR. RAEHL:  No.
                 DR. KONSTAM:  No.
                 DR. RODEN:  No.
                 DR MASSIE:  Did we get all the way up?  Okay.  
                 All right, question 5, and Ray, you can at some
        point tell me if there are other questions we can skip
        along the way.  
                 Was there statistically significant effect
        found for hospitalizations for cardiovascular causes in
        V-HeFT I?  
                 DR. LINDENFELD:  No.
                 DR. MASSIE:  Is there any discussion?
                 DR. LINDENFELD:  I think it was clearly no.
                 DR. MASSIE:  I guess rather than try to find if
        there is a consensus, we will just vote.  
                 Cindy, why don't you start.  Oh, I am not sure
        you were here for all those data actually.  You can abstain
        if you weren't here for that.  We are in hospitalizations.
                 DR. GRINES:  Actually I did miss that.
                 DR. MASSIE:  I think you weren't there. 
                 Udho?
                 DR. THADANI:  I am not convinced.  No.
                 DR. MASSIE:  Ralph?
                 DR. DiMARCO:  No
                 DR. D'AGOSTINO:  No.
                 DR. BORER:  No.
                 DR. LINDENFELD:  No.
                 DR. MOYE:  No.
                 DR. MASSIE:  Cynthia?
                 DR. RAEHL:  I need a minute.
                 DR. RODEN:  We don't have the data.
                 DR. WEBER:  Yes, where is this stuff?
                 DR. MASSIE:  The data was presented, I believe,
        for hospitalizations, or at least it was in the package. 
        The hospitalizations were not different.
                 DR. COHN:  Yes.  No, we didn't claim any --
                 DR. THADANI:  Actually it's on FDA packet also,
        page 18 and 19.
                 DR. LINDENFELD:  There's no disagreement about
        hospitalizations.
                 DR. MASSIE:  All right.  Is everybody voting? 
        Well, keep going.  
                 DR. WEBER:  No.
                 DR. RAEHL:  No.
                 DR. KONSTAM:  No.
                 DR. RODEN:  No.
                 DR. MASSIE:  One abstention.  Right.
                 There were three measures of exercise tolerance
        in V-HeFT I.  For which of these were there statistically
        significant treatment effects?  These are the maximum
        oxygen consumption, the total duration of symptom-limited
        exercise, and submaximal exercise duration.  
                 Do you want to comment on these?
                 DR. LINDENDFELD:  I think that total duration
        was not significant, and the submaximal exercise duration,
        there wasn't enough data really to evaluate that.  Maximum
        oxygen consumption is certainly of borderline significance. 
        Some points are positive and some are not, so overall I
        don't think there is a definite overall improvement,
        although it is very suggestive.  Strong trends.
                 DR. MASSIE:  Lem, any comment?
                 DR. MOYE:  I think if you consider the comments
        we made about corrections that came out in questions 1
        through 3, then I look at question 6 about statistically
        significant.  I am thinking statistically significant after
        making the kinds of adjustments that we have discussed. 
        And after making those adjustments, I don't see that we can
        say that any of these are significant.
                 DR. MASSIE:  I haven't put Bob on the line
        since he hadn't voted, and you are not allowed to vote.  Do
        you think there is a significant effect on any of the
        exercise measurements?  
                 DR. CODY:  (Inaudible.)
                 DR. MASSIE:  Jeff?
                 DR. BORER:  No.
                 DR. MASSIE:  Okay, well, JoAnn has pointed out
        that the only one probably worth voting on is the maximum
        oxygen consumption.  Maybe we can start down all the way on
        the left.
                 DR. THADANI:  Again, Barry, that is only on one
        point in time, of all the different points.
                 DR. MASSIE:  I think the question is, do we
        feel that there is a significant effect on maximum oxygen
        consumption.  I guess our thinking should take into
        consideration the various time points and what was found.
                 Dan, you want to start us off on that?
                 DR. RODEN:  Can you state the question?
                 DR. MASSIE:  Yes.  The question is, was there a
        significant treatment effect on maximum oxygen consumption
        at peak exercise during a maximum exercise tolerance test?
                 DR. RODEN:  Yes.
                 DR. KONSTAM:  I am not sure.  Can we hear the
        statisticians' view of this first?
                 DR. MASSIE:  We heard Lem.  We didn't put Ralph
        on line.
                 DR. D'AGOSTINO:  If you want to just say let's
        look at this particular variable -- forget for the moment
        the multiple testing and so forth -- I had asked the
        question, okay are you going to do lots of different time
        points.  Do you see a consistency in significance across
        those time points, and you see a couple here and there and
        they sort of fade away.  So, even in this situation of not
        getting caught up with the multiple testing, the data is
        not overwhelming.  
                 If you now want to add to the fact that this is
        in the presence of all these other tests going on, I don't
        see this is demonstrating significance.
                 DR. MASSIE:  Jay showed us the 3 and 6-month
        data which he said in itself would be enough to -- or was
        that in V-HeFT II?
                 DR. COHN:  The V-HeFT II data.  
                 DR. MASSIE:  In V-HeFT I it was the 12-month
        point.
                 DR. THADANI:  It's on page 17 of the FDA
        document.  There is only one point which --
                 DR. MASSIE:  Yes?
                 DR. RODEN:  I was looking at V-HeFT II.
                 DR. MASSIE:  Let's start all over.
                 DR. RODEN:  Starting all over.  That's B20 in
        the package.  For V-HeFT I I think the answer is no.
                 DR. MASSIE:  Okay, no.
                 DR. KONSTAM:  No.
                 DR. RAEHL:  No.
                 DR. WEBER:  Yes, I guess I would say no too,
        but you look long and hard at this and I guess we are going
        to have the opportunity of revisiting this when we look at
        V-HeFT II and putting them both together.  So, it's no for
        the moment, is my vote.
                 DR. MOYE:  No.
                 DR. LINDENFELD:  No.
                 DR. MASSIE:  No.
                 DR. DiMARCO:  No.
                 DR. THADANI:  No.
                 DR. GRINES:  No.
                 DR. BORER:  No.
                 DR. D'AGOSTINO:  No twice.
                 DR. TEMPLE:  We didn't actually discuss this,
        but I have a side question for the committee that sooner or
        later I think we will have to answer, which is, what would
        a change in maximum oxygen consumption imply to the
        committee in the absence of a change in exercise tolerance? 
        Two different measures of the same thing.
                 I don't believe we have ever relied on oxygen
        consumption as a measure of a symptomatic improvement in
        heart failure, but it wouldn't be --
                 DR. MASSIE:  Well, let me just make a quick
        answer to that.  I know we have been here and we have
        looked at studies where they have had both, but the oxygen
        consumption was always the sub-study of overall exercise
        tolerance.  In this particular protocol, oxygen consumption
        is clearly identified as the primary measure.  So, I think
        following the trend, I would take what the protocol tells
        us.  
                 But if they, for instance, said both equally,
        how would we weigh one versus the other? 
                 DR. TEMPLE:  No, I am asking whether you think
        that is a -- well, you can defer this until afterward, but
        sooner or later we probably ought to touch on it.  Is it a
        suitable measure of symptomatic improvement?  It is an
        unfamiliar measure of symptomatic improvement, that's for
        sure, but it still might be reasonable.  Sooner or later I
        think we would like to hear what you think about that, but
        you don't have to do it now.
                 DR. MASSIE:  Okay, well, maybe we won't do it
        now.
                 Was there a statistically significant effect
        found for quality of life in V-HeFT I?  As I remember, we
        should probably skip that because the sponsors didn't feel
        they had seen one either.  The measurements were not very
        precise.
                 Number 8, was there a statistically significant
        effect found for left ventricular ejection fraction in V-HeFT I?  Maybe we'll start with JoAnn.
                 DR. LINDENFELD:  Yes, I think there was.
                 DR. MASSIE:  Not so much for voting, but I
        guess discussion purposes.
                 DR. LINDENFELD:  Yes, I think at both 8 weeks
        and a year there was a significant effect.
                 DR. MASSIE:  Anybody have any other comments?
                 DR. KONSTAM:  I'd like a little bit more
        clarification of this.  Was this one of the predefined
        secondary endpoints?
                 DR. MASSIE:  I think it was one of the
        predefined -- well, the secondary of the primaries.
                 DR. LINDENFELD:  Yes, the primaries.
                 DR. MASSIE:  It was a primary endpoint but
        we've all I think judged it to be below mortality, which
        was mentioned so often.
                 DR. KONSTAM:  Okay, so in that light, I am not
        sure precisely what this question is asking.  Is it asking
        that question after the correction for the fact that there
        are five other primary endpoints?
                 DR. LIPICKY:  That is correct.
                 DR. MASSIE:  That is correct.  But we are not
        voting now.  I think this is worthy of some discussion and
        I see Dan has his hand up too.
                 DR. RODEN:  Ray, do you want to put in the
        labeling, or does somebody want to have this drug indicated
        to improve ejection fraction?
                 DR. LIPICKY:  No.  I don't think it is a matter
        of what the labeling would be or the approval.  I
        understand that.  I understand it was a facetious question. 
        But the thing that this was trying to elicit was, what are
        the positive things you can take away from the trial, and
        the reasons why one would say that the trial was positive.
                 MS. STANDAERT:  Ray, we can't hear you.
                 DR. LIPICKY:  Oh, sorry.  
                 The reason for the question was to see what the
        positive things are that one could take away from the
        trial, and what it would be labeled for would come later
        once one finally came to the conclusion that the trials
        found something.
                 DR. MASSIE:  So, I guess the question is sort
        of a totality.  Do we think there is an improvement in the
        ejection fraction and that thought should include all the
        provisos as to whether we should even be looking at it,
        because Lem would tell us we should not be looking at it, I
        guess.
                 DR. LIPICKY:  No.  What did I say that made you
        say that?
                 DR. MASSIE:  I don't know.
                 I think when somebody said after all the
        correction and all the rest --
                 DR. LIPICKY:  Yes.  Well, I think all of that
        is true.  That is, would you look at this trial, and on the
        basis of the result say that there was an effect on
        ejection fraction found with some degree of certainty.  And
        that includes everything that we have been talking about
        all the way along.
                 DR. FISHER:  Could I make one technical
        comment, Barry?  The statisticians might like to look on
        page A130 of appendix 4 of the report because I did a
        generalized estimated equation analyses with a variety of
        different models which incorporate all the time points at
        once.  
                 DR. MASSIE:  Do you have a page number?
                 DR. FISHER:  Yes, A130.
                 The reason for pointing this out is it relates
        to the relative strength of effect because we have been
        talking a lot about adjustments and things.
                 DR. MASSIE: I would guess I would interpret
        this question, or at least I would vote on this question,
        saying that one could agree that the ejection fraction has
        been changed, and not agree that that makes it a positive
        trial.  Is that fair?
                 DR. LINDENFELD:  Yes.
                 DR. LIPICKY:  Sure.
                 DR. KONSAM:  There are a couple of different
        dimensions to this discussion.  One of them is what exactly
        are we being asked, and is it a purely mathematical
        statistical question.  And if that's the case, I might as
        well pass, and I think a lot of the other people on the
        panel would pass and just defer to the statisticians to
        reach a consensus about the mathematics.
                 I guess I would ask Ray, is there a question
        beyond that?  Is there a question that you are asking the
        clinically oriented reviewers or experts to then look back
        at the data after the statistical mathematical analysis and
        ask, okay, do you have reason to believe it now in the
        context of the mathematics, which is a different sort of
        question.
                 DR. DiMARCO:  I'd like to second Dr. Konstam
        there.  It would be hard for me as a clinician to overrule
        our two statistical consultants who told me it is hard to
        find anything statistically positive in this trial.  You
        know, and the question comes up, if you word it as, is it
        statistically significant, we have already said it is not,
        essentially.
                 DR. MASSIE:  No, I don't think we have.  Not
        for ejection fraction.
                 Bob has got his hand waving.
                 DR. TEMPLE:  I didn't hear any reservations
        from the biostatisticians about ejection fraction.  It's
        significant at four zeros.  
                 Maybe you'll tell us you don't like the way we
        put the questions, but this question was to say, is that
        real.  Not, is it valuable, is it a basis for claims, is it
        a basis for labeling.  None of that stuff.  That all comes
        later.  This is, did it happen.
                 DR. KONSTAM:  But I think that is important
        generally with regard to all of these questions because I
        find myself then, after we ask the purely statistical
        question, going back and looking at it again and seeing if
        there's any reason that I would believe, based on
        pathophysiology, clinical insight, whatever.  That maybe it
        is a marginally mathematically evident piece of information
        and I believe it because it fits a paradigm that I have. 
        And if that is the question, then we could add insight to
        that.
                 DR. LIPICKY:  Fine.  Perhaps all of these
        questions should be re-worded then and take statistically
        significant away and say, do you believe it?  Is this real?
                 But, you see, the problem is, if you can answer
        that question outside of the realm of statistical
        significance, I wonder how you can do that.
                 DR. KONSTAM:  I have thought about this, and I
        think what you do is you bring in the questions about does
        it fit a pathophysiologic paradigm.  Does it fit based on
        other information that you bring to bear that is not
        mathematical?
                 DR. LIPICKY:  Right, but if the statisticians
        said that this has a p of .5 and it fit your model, you'd
        still think it was real?
                 DR. KONSTAM:  Not at all.  But if the
        mathematics put it in a marginal zone then I think I would
        draw upon that set of information --
                 DR. LIPICKY:  Fine.  So, answer this question
        in terms of whether you believe it.  Is this effect real?
                 DR. MASSIE:  And I think that is what we have
        been trying to do, although I guess there is a varying
        level of how people answer these questions in terms of that
        type of thinking.  
                 Lem says we shouldn't think about this.  I
        think he means that in a different type of context than can
        we look at these numbers and decide.  I shouldn't be
        reading into what Lem is saying.
                 But does this make a trial positive is one
        question.  Do we believe that there is a real effect on
        ejection fraction is a second question.
                 DR. LIPICKY:  It should not be looked at from
        the vantage point of, does this make a positive trial.  We
        have never asked you to count the number of positive
        trials.  So whether you think this is a positive trial or
        not is irrelevant.
                 DR. COHN:  But I'd ask you, Barry, in light of
        this discussion, to go back to the mortality issue and ask
        the panel whether they think the mortality reduction is
        real, even if not statistically significant by nominal p
        values because that is clearly the question that is being
        proposed by the agency to find out.
                 The p value question only can depend upon Lem
        and Ralph, but the implication of the reduction of
        mortality requires the clinical judgment that Marvin has
        identified.
                 DR. LIPICKY:  I'll second that.
                 DR. MASSIE:  Okay.
                 DR. TEMPLE:  Barry, I want to object.  I'm
        sorry.  We are dancing with words here and it is
        treacherous.
                 If the committee wants to tell us, yes, I sort
        of believe it, I can't quite tell you why, the p values are
        all over the map, that is not very helpful to us because
        that's information we can't use.  You can't approve a drug
        because someone has an emotional reaction to it.
                 These questions all bear on a seasoned
        judgment, but it's a judgment based on statistical and
        other considerations.  
                 I just want to make one observation.  We have a
        large number of biostatisticians and we think that we share
        these judgments about -- we clinicians, I mean -- 
        adjustments and things like that with the biostatisticians. 
        They know the math in ways we can't even begin to fathom,
        but how many endpoints are reasonable and things like that
        are questions that clinicians -- that we feel we have to
        deal with, and we've never been told by biostatisticians
        that we don't dare think about those things.
                 So, too much helplessness in the face of good
        statisticians is not necessary.  These are all things that
        intelligent people skilled in study design can think about.
                 So, the question here was, given the p value
        .0001 for the ejection fraction data, is there a question
        about whether that happened?  Later on you get to, suppose
        it did happen?  Who cares?  That is a different, perfectly
        important question.  
                 But at this point you don't have to really
        defer to -- you can reach an answer with the advice of
        your --
                 DR. MASSIE:  I think the reason why this
        question was sort of re-opened is that it may be that some
        of the newer members of the committee, which is almost
        everybody, were not thinking along the same wavelengths.  I
        think that is an important thing to clarify.
                 I think when I would think of these questions,
        yes, you would take the data from the statisticians, you
        weigh it against what you've seen in the midst of all this
        morass of information, and you make a clinical judgment. 
        That in fact is how I voted already, but I am not sure
        everybody else did.
                 DR. TEMPLE:  The formulation I had trouble with
        was, apart from statistical considerations, do you think
        this works?  The clinicians aren't supposed to be apart
        from the statistical --
                 DR. KONSTAM:  Dr. Temple, can I just respond
        to --
                 DR. TEMPLE:  -- supposed to be in light of
        statistical.
                 DR. MASSIE:  Right.  Well, is that what you
        meant?
                 DR. KONSTAM:  Can I respond to that?  First of
        all, I agree with you completely.  None of us should be
        saying things that we can't defend by something.  So nobody
        just sort of looks at it and I can't tell you why. 
        Obviously we need to tell you why.
                 The second thing is, I guess all of us feel,
        okay what do you want from us.  I think that there is
        confusion.  I think Barry said it, about is this a purely
        mathematical question that we are being asked, or is it a
        question that is based on the mathematics at first and then
        interpreted with an eye to pathophysiology and clinical
        judgment.  It sounds like you want the latter.
                 Where this really does come to bear, based on
        some of the discussions among the statisticians that I have
        heard, there are circumstances of some very, very
        compelling findings that seem very, very compelling to us,
        and some of the statisticians say, just don't look at it. 
        I can't deal with this.  It's a post hoc analysis and yet
        it's an enormous finding.
                 Then I think that is the circumstance where we
        might want to say, all right, but do you believe it anyway,
        and why.
                 DR. MASSIE:  Ralph.
                 DR. D'AGOSTINO:  I think what you just said is
        very important, and what I think I am saying is that that
        is not present in this study with regard to mortality. 
        When we were talking about the adjustments, the questions
        1, 2, and 3, they were focused on mortality.  No matter how
        you look at the statistical procedures that they used and
        put forth to us, any kind of adjustment takes them over.
                 With this particular one, I think any kind of
        adjustment still keeps it in the statistically significant. 
        We are moving very quickly through these, but don't carry
        with you that I said or that Lem said that everything is
        out now because of the multiple testing.  This is very
        significant from a statistics point of view.  Then there is
        the other question.
                 DR. MOYE:  Well, certainly, if you just look at
        the nominal p value.  If you just want to confine your view
        to the nominal p value, as though that was the only
        evaluation done in this program, then you have to argue for
        its statistical significance, but that is not the only
        evaluation done in the program.
                 The question is, what does the p value mean?  I
        mean, if all you will do is look at these nominal p values
        and say, yes, they are significant because they are less
        than .05 or less than .01 or .001, then the overall alpha
        means nothing with that interpretation.
                 I guess I insist that the overall alpha is very
        important.  
                 DR. D'AGOSTINO:  No, I am not disagreeing.  I
        am saying that if you apply all the discussion I had a
        moment ago where I was being very loose about it, I think
        that you have a very small p to begin with.  As you
        multiply it for other things, you still have a small p. 
        And I agree with you.  I am not saying, I don't think
        anybody is saying that you should look at this as it stands
        by itself.
                 What I am saying is, when you make all those
        adjustments, we make a number of those adjustments, this
        would probably still withstand the rigor of .05.
                 DR. MASSIE:  Yes.  Let's call this question. 
        Ralph, this is the ejection fraction question.  Is there a
        significant effect on ejection fraction shown in this
        trial?
                 DR. D'AGOSTINO:  Yes.
                 DR. BORER:  Yes, I think there is.  
                 I would like to add one thing, just a plea to
        Jay.  Anywhere else in the world you can say whatever you
        want, but in this one building, just building 10 here at
        the NIH, please don't call the technique you use to measure
        it MUGA.
                 (Laughter.)
                 DR. MASSIE:  With that comment, Cindy?
                 DR. GRINES:  Yes, it's significant.
                 DR. THADANI:  Yes.  
                 DR. DiMARCO:  Yes.
                 DR. MASSIE:  Yes.
                 DR. LINDENFELD:  Yes.
                 DR. MOYE:  No.
                 DR. WEBER:  Yes.
                 DR. RAEHL:  Yes.
                 DR. KONSTAM:  I'm not sure.  Let me just
        clarify my answer.                                     I'm not sure on the basis of what I have heard from
        the statisticians whether it is statistically significant
        or not.
                 DR. MOYE:  I guess we disagree.   We have a
        different point of view.
                 DR. KONSTAM:  Exactly.  Therefore, I --
                 DR. MASSIE:  By the way, I phrased the question
        without the word "statistically."
                 DR. KONSTAM:  Good.  So, I believe the data.  I
        think there is an increase in ejection fraction.
                 DR. RODEN:  I think ejection fraction rises.
                 (Laughter.)
                 DR. MASSIE:  Ray, I'm sorry to have to ask
        this.  Do you want us to vote on whether we think there is
        a significant effect on mortality without the "statistical"
        in there?
                 DR. LIPICKY:  I think I would like to hear a
        yes or no vote that takes away the statistically
        significant part.  Did V-HeFT show an effect on mortality
        compared to placebo?  This is the kind of feeling question,
        so you don't have to break it up into 2-year and total
        mortality.  Was there an observation that makes you believe
        there was a mortality effect seen?
                 DR. KONSTAM:  Now, Ray, could you give us some
        kind of idea what level of certainty you would like to see.
                 DR. LIPICKY:  Statistically significant. 
                 (Laughter.)
                 DR. KONSTAM:  60/40?
                 DR. MASSIE:  Are you convinced that there is an
        effect on mortality?  I think that is the question.
                 DR. LIPICKY:  You have already made it very
        clear what you think the statisticians think.  So, this
        question is asking you what you think, so that we have it
        clearly --
                 DR. KONSTAM:  Is it pretty clear to us that
        there is an effect on survival.
                 DR. LIPICKY:  Right.  Was a survival effect
        shown.
                 DR. MOYE:  Well, we have to be careful about
        that.
                 DR. MASSIE:  I don't think we should say pretty
        clear.  I think you want to know whether we are convinced
        that there was a mortality effect.
                 DR. LIPICKY:  That the trial found an effect.
                 DR. MOYE:  But there is no question that in
        V-HeFT I more patients died on placebo than died on the
        hydralazine-isosorbide dinitrate.  There is no question
        about that.  That's the data.  The issue is, what does that
        mean for the population at large?
                 DR. LIPICKY:  Well, yes and no.  Well, let me
        be sure that I am not doing something totally crazy. 
                 The committee very clearly indicated what it
        thought the study showed in a quantitative way, that is, in
        a carefully considered statistical fashion.
                 The question that I want the committee to
        address now with just a yes and no vote, is, even though
        they think that, what does their gut say?  And I don't know
        that we'll pay any attention to your gut, and probably
        should not, but because this discussion is going on, I
        would just like to know what the result of that vote would
        be.
                 DR. MASSIE:  Can I rephrase the question, then? 
        Because I think we have to have some quantitative sense.
                 The question I would ask is, if this study was
        repeated 100 times, are we --
                 DR. LIPICKY:  I think that is a reasonable
        question.  Would you expect to find this many times?
                 DR. COHN:  You know, it's more than gut, Ray,
        because we're using an arbitrary p cutoff of .05 and our
        statisticians -- or whatever number they are using, because
        it gives us that greater confidence in the result.  But
        even then we are only dealing with 19 out of 20
        possibilities.  And if it is .07 or .08, does that mean
        it's the same as .9?  No, it doesn't.
                 DR. MASSIE:  Well, we can't rediscover total
        philosophy, I think, but I think this is probably an
        important sort of way for Ray to get some information from
        the committee which is, do we think that if we did this
        trial 100 times, that at least 95 percent of the time we
        would show a convincing level of reduction in mortality. 
        Is that fair enough, Ray?
                 DR. LIPICKY:  It is for me.
                 DR. KONSTAM:  Can I just throw one other thing
        in?  I guess one might ask, is it convincing to us enough
        as a very well informed clinician.  Would you use it in
        clinical practice based on everything you know?  And to me
        when you get up around, let's say -- just to set different
        standards, when you get up around the 60/40, 70/30 level,
        as long as you are pretty convinced it's safe, you would
        probably use it.
                 Now, it sounds to me that the FDA requires a
        higher level of certainty than that.
                 DR. LIPICKY:  Well, you have responded to the
        question of statistical significance.  We are not
        interested in whether or not you would use it.  We are
        interested in you as a scientist and investigator.  Are you
        convinced that this trial, from that vantage point, if
        repeated, would find an effect, that again you would
        believe?  That's the question.
                 Certainly in the practice of medicine one uses
        things that one has absolutely no knowledge about at all. 
        I know that.
                 DR. MASSIE:  I think we need to move on.  I
        think we need to give this opinion.  Everybody should look
        forward to question 20, which is whether BiDil should be
        approved for heart failure.  That is certainly going to be
        something where if there is a different answer to this
        question from the statistical question, then people will
        have to deal with that somehow.
                 I am going to start down there with Cindy.  Do
        you want to answer this more clinically oriented question? 
        Are you convinced that this drug has a significant, but not
        necessarily statistically significant, effect on mortality?
                 DR. GRINES:  We are back to the beginning of
        the questions?
                 DR. MASSIE:  Yes.
                 DR. GRINES:  With V-HeFT I?  Actually that is
        what we have been discussing here, and I think that there
        does appear to be a clinically significant difference in
        mortality.  Whether it meets the biostatistical criteria,
        I'm not capable of answering that.
                 DR. MASSIE:  Udho?
                 DR. THADANI:  I think as an investigator and a
        clinician, I am having problems.  The trend is in the right
        direction but I am not convinced that it is significant. 
        So if you would repeat the experiment, it may not bear out
        again.
                 DR. MASSIE:  Ralph?
                 DR. D'AGOSTINO:  Do you want a comment or do
        you want a vote?
                 DR. MASSIE:  I want an answer.  
                 DR. D'AGOSTINO:  I just don't see how we can
        separate all the previous discussion.  I think there is no
        way of knowing.  I think the answer you just got was the
        correct answer.  There is no way of knowing.  It remains to
        be seen.
                 DR. MASSIE:  That's a no, I think.  
                 Jeff?
                 DR. LIPICKY:  Was that a yes or no?
                 DR. MASSIE:  That was a no.  He doesn't feel --
        he's not convinced.  
                 DR. BORER:  I would say no also, and I would
        like to amplify a little bit.  I think that if the study
        were repeated, it's more likely that you would come up with
        a similar answer than that you wouldn't come up with a
        similar answer.  But the data that have been presented
        leave me without a reasonable assurance that you will come
        up on the second try with the same kind of result.
                 Certainly if I were a clinician faced with a
        patient with congestive heart failure who couldn't take ACE
        inhibitors, seeing these data and seeing that they sort of
        trend in the right direction and there is nothing to
        suggest that they do something bad to people, and the
        condition is a horrible one with a terrible outcome, I
        would probably go with this combination of drugs, even
        though I don't have the strongest of data to support my
        doing that because I don't have any other options and it's
        a bad situation and I'm not doing much harm that I can see.
                 But as a regulatory issue, I have to say no.
                 DR. LIPICKY:  What do you mean, Jeff?  You have
        sucrose sitting on the shelf.
                 DR. BORER:  But I have no data about sucrose.
                 DR. LIPICKY:  Yes, you do.  Right there in this
        trial.
                 DR. BORER:  They don't even trend in the right
        direction.
                 DR.  MASSIE:  Since this is an opinion, we
        should get Bob's opinion, even if he can't vote.
                 DR. CODY:  We're talking about V-HeFT I and not
        the drugs themselves overall.  We're talking about this
        study.  It gets into temporal issues, when the study was
        conducted, et cetera. 
                 I guess all I could say is, when this study
        came out, it influenced my treatment practices.  So, did I
        think it was significant?  Yes.
                 DR. DiMARCO:  I agree with Dr. Borer, except I
        am going to answer yes instead of no, because I just think
        the level of certainty I have is much less than I usually
        see for trials that are submitted for approval.
                 DR. MASSIE:  I thought Jeff said it very well,
        too, but I am going to vote no because I do believe that
        "convinced" for me is informed by statisticians and also by
        whether I think 95 times out of 100 the same thing would
        happen, and I am not convinced that that would be the case.
                 DR. LINDENFELD:  I am not convinced it would be
        95 out of 100, although I do believe it might be 70/30.
                 DR. MASSIE:  Wait.  Is that a yes or a no?
                 DR. LINDENFELD:  It's a no.
                 DR. MOYE:  I think all roads lead to the
        statistics here.  Whether you say statistically
        significant, whether you say you are sampling from the
        population at large, they all lead to statistics and the
        answer is still no.
                 DR. WEBER:  Well, I have a slightly different
        point of view.  First of all, I agree with what Lem and
        Ralph have said about the statistics.  I think we have to
        acknowledge that there is a right way to do them, and that
        at the end of play we didn't quite have a statistically
        significant result, but it wasn't a huge deviation from
        that.
                 I look at the survival in V-HeFT I on the
        combination of hydralazine and isosorbide dinitrate.  I
        look at the data from V-HeFT II.  It gives me reassurance
        that that first line is real.
                 DR. MASSIE:  No, you're not looking at V-HeFT
        II.
                 DR. WEBER:  No, but I know from a collateral
        source that this line is probably realistic.  It separates
        from two other lines on the same graph.  As far as I am
        concerned, whether it is 95 percent or 93 percent, I
        believe that it is clinically meaningful and I would vote
        yes.
                 DR. MASSIE:  Cynthia.
                 DR. RAEHL:  One, I don't believe in the
        infallibility of statistics and that all things lead to
        that.  Looking at the collection of the data, I would
        suggest, yes, I believe this does suggest a very strong
        trend.
                 DR. KONSTAM:  To the question about whether I
        am convinced that this is right and reproducible, the
        answer is no.  I would add, however, that it considerably
        surpasses my usual threshold of evidence that I require to
        recommend to clinicians to use, so I would readily use it
        in clinical practice.  But am I convinced it's right?  No.
                 DR. RODEN:  I think the reason we are having
        difficulty is because if it's real, it's a small effect. 
        It's not a huge effect, and that is why, given what the
        statisticians have told us and given my bias about a small
        effect, I vote no.
                 DR. MASSIE:  Okay, I hope that nobody remembers
        we ever had this discussion when we move on to regulatory
        things.
                 (Laughter.)  
                 DR. MASSIE:  But I think it's very important
        because there is a paranoia that we are marionettes and
        statisticians tell us what to do, and I think the answer is
        we need to think for ourselves also but listen.
                 With that comment, I think we are down to --
        where are we?  Nine.  Headache and blood pressure are
        consistent.  Do you want us to continue with that?
                 DR. LIPICKY:  No, you can skip that.
                 DR. MASSIE:  Moving on to V-HeFT II, and again,
        Ray or Bob, you can tell us if we don't need to keep on
        going on every question.
                 V-HeFT II had no placebo group.  The division
        and the advisory committee have held a successful active
        comparator trial requires one to conclude that new
        treatment would have beaten placebo had there been a
        placebo group, and that the estimated effect size of the
        new treatment is not less than half of the effect size for
        the comparator agent.
                 Now, I know that Bob Fenichel has some
        comments.  I think we don't have a great deal of time, but
        having spent 12 hours of my life listening to this
        discussion and now being the only one left on the committee
        that did, there actually has been a discussion and some
        standards that the FDA has recommended, at least, to
        sponsors about what it might take to get a drug approved if
        there is no placebo group in the trial.  I wonder whether
        maybe in three minutes you could summarize that discussion.
                 DR. LIPICKY:  I don't think he needs to do
        anything yet.  
                 DR. MASSIE:  Yet.  Okay.
                 DR. LIPICKY:  Let's see if you understand.
                 DR. MASSIE:  Okay.  One way in which it could
        be concluded that hydralazine-isosorbide was superior to
        placebo would be if the combination were superior to
        Enalapril in V-HeFT II.  Was hydralazine-isosorbide
        dinitrate superior to Enalapril for any of the mortality or
        exercise endpoints?
                 Okay, any discussion?  How about JoAnn?
                 DR. LINDENDFELD:  No, I don't believe so. 
        There were no overall definite benefits.
                 DR. MASSIE:  Any other comments or discussion
        from the committee? 
                 DR. RODEN:  The data are more compelling here
        than they were in V-HeFT I.
                 DR. MASSIE:  You have to talk louder or more
        directly.
                 DR. RODEN:  The data looked more compelling. 
        The graphs looked nicer in V-HeFT II than they do in V-HeFT
        I.  So, I would be interested in the statistical opinion
        with regard to, for example, the change in VO2 or the
        change in -- what was the other one -- change in ejection
        fraction.
                 DR. MASSIE:  Change in VO2 or change in
        ejection fraction.  Dan is not sure that he hasn't seen
        something there, I guess.
                 DR. RODEN:  Graph B27, for example, in the book
        looks more convincing than in V-HeFT I.  
                 DR. MASSIE:  Okay, any other comments?  Dan
        wanted to hear from -- 
                 DR. RODEN:  From Ralph or Lem.
                 DR. MASSIE:  So, there are the two pieces of
        data we have.  Since we know there was not an improvement
        in mortality compared to Enalapril, these are the two.
                 Any other comments?  I think we do need to hear
        from --
                 DR. RODEN:  I think this is an important issue
        because if in fact an improvement in symptoms has been
        demonstrated using that kind of measure, then it will
        affect the way we vote on your last question.  So, Lem or
        Ralph?
                 DR. MASSIE:  Lem?
                 DR. MOYE:  I guess I am furiously calculating
        here.  This is another study now where you do have a
        positive endpoint on mortality.  We're talking about V-HeFT
        II.  Right?  
                 DR. MASSIE:  
                 DR. MOYE:  But it is a positive endpoint in --
                 DR. KONSTAM:  In the other direction.
                 DR. D'AGOSTINO:  It is in the wrong direction. 
        The competitor beat out the product.  It went in the wrong
        direction.
                 DR. MOYE:  Right, and I guess that is what I'm
        trying to work through now.  
                 I would say that perhaps an argument here is
        admissible.  At least from my alpha spending function, it
        would be admissible to consider it.
                 DR. MASSIE:  Ralph?
                 DR. D'AGOSTINO:  Are we going to go item by
        item?  It just went in the wrong direction, so --
                 DR. MASSIE:  Well, mortality we are not
        discussing, but what the question asks if I can still dig
        it up.  
                 DR. D'AGOSTINO:   Which one?
                 DR. MASSIE:  On exercise and presumably
        ejection fraction, you also concluded -- well --
                 DR. THADANI:  You skipped 10 and 11.  
                 DR. MASSIE:  No, I thought I was reading 10. 
        Mortality or exercise, right.  
                 In other words, the question is, since there is
        no placebo group, how do we interpret it?  And the question
        says, if the drug, BiDil, beat what we think to be an
        effective comparator, that would be a positive trial.
                 It did not for mortality.  So, we're talking
        about exercise.
                 DR. THADANI:  Barry, before you go further, can
        you allude one thing?  Since there is no placebo, we are
        already saying that we are not going to compare it with
        historical placebo.  I think we should establish that,
        because our problems with that --
                 DR. MASSIE:  No, we haven't said that at all.
                 DR. THADANI:  No, but I am just saying, in
        order to make a rational decision, since there is no
        placebo, I think there are two active controls and it
        happened that ISDN-hydralazine was inferior to Enalapril. 
        So as far as mortality, I think we have to accept that. 
        Right?
                 DR. MASSIE:  Right.  What they are asking is,
        even though it was inferior to mortality, was it superior
        to Enalapril for exercise?
                 DR. CODY:  In terms of exercise time or O2?
                 DR. MASSIE:  Well, I think that they wisely
        said exercise endpoints.  I assume that that was written
        with some intention.  
                 DR. LIPICKY:  That was written intentionally
        that way, yes.  You'll have to decide.
                 DR. D'AGOSTINO:  I'm not at all convinced by
        any of the data I see before me.  If it is a blanket
        answer, I would say no.
                 DR. MASSIE:  Bob?  Jeff?  You're not convinced
        either?
                 DR. CODY:  No, not on the O2s.
                 DR. MASSIE:  Since as I understand there was no
        significant difference on the other exercise endpoints, it
        really is the O2s we are talking about.  
                 Any other comments on this?
                 DR. RODEN:  But you didn't see data on the
        other exercise secondary endpoints.  So, there is no
        difference in exercise time or other endpoints, other
        secondary endpoints, Jay.
                 DR. COHN:  All the exercise endpoints trended
        in the same direction.  The primary exercise endpoint was
        peak VO2 in this trial, and that is the one that achieved a
        statistically significant benefit of H/ISDN at 3 and 6
        months.
                 Now, looking at the whole curves, of course,
        one as a statistician might raise issue about using those
        two points and disregarding the rest of the curves, but you
        must recognize as an agency that up to 6 months is the only
        data you have ever seen before.  So, based upon 3 and 6
        months, you would have approved this drug on the basis of
        better exercise, peak VO2 than with the comparator agent,
        which was Enalapril.                                  
                 DR. KONSTAM:  Is there a statistical approach
        to determining whether the two curves differ from each
        other, and should that be applied?
                 DR. D'AGOSTINO:  If you have a question that
        says what happens in 6 months, that can be a very real
        question and you could apply a technique that solely
        focuses on that 6 months.  Or you could ask a question
        about the whole curve.  You may not want to ask the
        question about the whole curve.  It may just be in
        particular time points. 
                 I'm not looking at that particular time point
        and saying that's significant and therefore I really have
        to focus on it.  I'm looking at all of the measurements
        that I have before me.  I see something significant here. 
        It's kind of nice, but I have seen a lot of things that
        aren't significant, and why would I extract this one and
        believe in it?
                 So, I am not looking at the full curve.  I'm
        trying to look at these significant results in the context
        of all the other procedures that have been played here. 
                 I don't think there is any hope, if you compare
        those two curves.  You may have something if you focused on
        that beginning part of it.
                 DR. MOYE:  I would like to second what Ralph
        said and add just one other thing.  
                 This is difficult for me to interpret
        independent of mortality data because you are losing
        patients as you go along the follow-up time.  Maybe the
        patients that you were losing who were dying were ones who,
        if they had survived, would have had lower EF's.  So, I
        just have a difficult time trying to interpret this.
                 DR. MASSIE:  Yes, I think that's an important
        point.  I don't know if Jay has done this.
                 In the first study it was pretty clear that
        more people, if anything, were dying on hydralazine and
        isosorbide dinitrate, and therefore the placebo group might
        be at an advantage, if you look at exercise time.  In this,
        more patients died with hydralazine-isosorbide dinitrate.
                 Was a carry-forward analysis done?  In other
        words, in the people who died, did we look at their last
        exercise measurement and carry that forward through any of
        these endpoints?
                 DR. COHN:  Well, we don't like doing that
        because it really implies that patients would have stayed
        the same had they been alive, and the other alternative is
        to substitute obviously a low value for those who died.  I
        don't like doing that either because I think that obviously
        dilutes the data in a favorable direction.  But I can't
        believe it.
                 I think what we've learned since these trials
        have been done is that you would not choose to do prolonged
        exercise testing over a long period of time because of
        differential mortality, and that is why I focus on the 3
        and 6-month data because there was not differential
        mortality during those early time points when you can
        really evaluate the effect of the therapy on a non-mortality endpoint.
                 After 6 months you being to see a difference
        that makes it very difficult to interpret, and I am not
        sure how you do it.
                 DR. THADANI:  Barry, can I comment?  On the
        documents you were given from the FDA, if you look on page
        40, the middle paragraph, it says, "For exercise tolerance
        and other endpoints related to cardiac function,
        hydralazine-ISDN had very little advantage over Enalapril
        for maximum oxygen consumption.  Multivariate analysis
        showed no significant difference between the treatments."
                 So, I think I will go along with that because
        that's in your documents.  All of you have that.
                 DR. MASSIE:  What page is that?
                 DR. THADANI:  Page 40.  Under V-HeFT II, third
        paragraph.
                 DR. D'AGOSTINO:  I told you that without
        looking at the text.
                 DR. LIPICKY:  We can show you that analysis on
        a transparency, if you'd like.  I don't, unfortunately,
        know --
                 DR. BORER:  To be fair, that analysis is over
        the entire curve, which was the issue that is somewhat at
        issue.  
                 DR. LIPICKY:  Does anyone know the page number
        in the reviews where those tables appear?
                 DR. BORER:  Yes, the raw data, 32 and 33.
                 DR. THADANI:  And also the p values varied.
                 DR. TEMPLE:  Barry?
                 DR. MASSIE:  Yes, Bob?
                 DR. TEMPLE:  There's another problem with
        picking the 3 and 6-month time points.  If one had observed
        a benefit accrued only belatedly, one could think of a
        plausible reason for why that should occur because there is
        more time to prevent remodeling.  You can always think of a
        good reason for anything.  So, unless the 3 to 6 were
        specifically identified as the time points of interest, you
        have to worry that you are once again following your nose. 
        Always a problem.
                 DR. CODY:  Can I just amplify on my comments? 
        It has something to do with what you raised earlier.  
                 This slide shows the peak VO2's, and it assumes
        there was no difference statistically, even biologically,
        in the peak O2's at baseline.
                 The previous graph, which is B26, shows the
        mean change for the two groups.  There the outcome is a
        little bit different, certainly at least at 6 months.  I
        guess you'd have to wonder what would happen if a placebo
        group was in there.  Would it be negative at 3 and 6
        months, or would it fall between the groups?
                 So, given that we don't use peak VO2 all that
        much as an endpoint independent of exercise time, and with
        the understanding that 3 and 6 months is as long as perhaps
        a lot of other trials, so one has to be careful about
        putting too much weight on the absence of significance over
        time down the line, it still comes across to me as sort of
        a weak observation given that exercise time didn't change.
                 DR. MOYE:  I guess I would just say, putting
        together what Ralph has said about the concerns about the
        multiple time points, and also this differential censoring
        effect, where patients on the hydralazine-ISDN are more
        likely to die, and you don't know what their EF's would
        have been, I am inclined to vote that there is no
        significant effect here for the change over time.
                 DR. MASSIE:  I think there are a lot of
        questions, and the one that Bob brought up earlier is, if
        we were to agree that there is an increase in peak VO2,
        does that mean that patients feel better, because I guess
        that is why exercise came into play, as a quantitative
        measurement of symptoms.
                 There are the multiple points in time.  
                 I think it is not a clear-cut issue but I guess
        we need to vote on this.  In the absence of further
        comment, I think the way we should phrase the vote is, was
        hydralazine-isosorbide dinitrate superior to Enalapril for
        any exercise endpoint, or for exercise endpoints?
                 JoAnn, do you want to vote first?
                 DR. LINDENFELD:  If we're going to divide them
        up, I think it was significant for peak VO2 at 6 months. 
        The FDA analysis doesn't give it quite statistical
        significance at 6 months.  I think it was .1.  But the
        exercise time, and then I think the time and anaerobic
        threshold were not significant at all.
                 DR. MASSIE:  So that is a yes, that -- I think
        the way, if I can hazard to guess what Ray is asking, is,
        do we feel exercise capacity was improved in V-HeFT II?
                 DR. LIPICKY:  I'm sorry, I was talking to
        someone else when you were talking.
                 DR. MASSIE:  This question, since you didn't
        say VO2, are you asking us whether we think exercise
        capacity was improved in V-HeFT II?
                 DR. RODEN:  You are using exercise capacity in
        a sort of general way.  That's the way I interpret your
        question.  My answer is no.
                 DR. MASSIE:  We started down there.  We'll keep
        on coming from there.
                 DR. KONSTAM:  No.
                 DR. RAEHL:  No.
                 DR. WEBER:  No.  I'd agree with JoAnn.  I'm not
        sure what "in a general way" means but we do have these
        compelling data with the peak oxygen consumption at 3 and 6
        months.  So, to that extent, I would say yes, I think there
        is a difference between the two treatments, at least at
        that point of the study.
                 DR. MOYE:  No.
                 DR. LINDENFELD:  I think when you combine all
        three measurements of exercise capacity, the answer is no.
                 DR. MASSIE:  I think I'm going to have to vote
        yes, but there's an important proviso, which is the
        question I asked Jay.  I'd like to see whether the increase
        from rest to exercise in VO2 was improved significantly,
        and if it were, I would feel that is a quantitative measure
        of exercise capacity, but obviously we are not going to
        know that today.  But I will vote yes, assuming if it were
        ever to be examined, it were found to be positive in that
        manner.
                 DR. DiMARCO:  I vote yes for the 3 and 6-month
        time points, but I really can't make a decision about the
        rest of the study.
                 DR. THADANI:  My answer is no.  At 3 months
        it's significant, but the FDA analysis at 6 months, p is
        .11.  So, the answer is no.
                 DR. GRINES:  I vote yes for 3 and 6 months.
                 DR. BORER:  I would have to say no.  I have
        concern about the 3 and 6-month points too, and again, they
        sort of just make it statistically, according to the
        analyses we were given, but no adjustments were made.  The
        entire discussion we had before is applicable here, and the
        putative difference is relatively small.  So, my overall
        response is that the answer is no.
                 DR. D'AGOSTINO:  No.
                 DR. MASSIE:  We've got the vote.  Maybe we can
        gain some momentum here now.
                 If hydralazine-isosorbide dinitrate were not
        superior to Enalapril, it might still be superior to
        placebo.  11.1, the sponsor argues that an answer to that
        question would best be derived by comparing the
        hydralazine-isosorbide dinitrate group to the placebo group
        in V-HeFT I.  The division argues that the best comparison
        would be with the results of the SOLVD treatment trial,
        where the magnitude of the effect of Enalapril was
        demonstrated, or with a combination of the results of SOLVD
        treatment and V-HeFT I.  What is the appropriate placebo
        group for this comparison?
                 Any questions or comments?
                 DR. LIPICKY:  This is for mortality now.
                 DR. MASSIE:  Right.
                 DR. MOYE:  I guess I have to say I'm extremely
        discouraged by this question because I think that the
        analysis that is suggested here is incorrect.  We are
        talking essentially about historical controls, and they are
        so fatally flawed with differences in therapy, baseline
        therapy, and baseline characteristics for the groups that I
        don't think this question is addressable.
                 DR. D'AGOSTINO:  I feel like I am being asked
        if I should kill my brother or my sister. 
                 (Laughter.)  
                 DR. D'AGOSTINO:  I think both answers would be
        problematic. 
                 (Laughter.)
                 DR. THADANI:  I think, Barry, without having a
        placebo control, we can't guess anything.  The trial was
        done.  Enalapril was superior, and we ought to just leave
        it at that.  We can't presume what placebo would have done. 
        It could have gone in any direction, so we can't use
        historical controls.
                 DR. MASSIE:  Well, I guess I need to raise the
        question that the agency is probably asking us not so much
        about this specific experience, perhaps, but we are in a
        day where there will be uncontrolled trials, and the
        division has sponsored a meeting where that has been
        discussed and how to imply things.  It was in the context
        of thrombolytic therapy where it wasn't possible.
                 DR. LIPICKY:  Barry, that's correct, but you
        have enough drug to consider.  So, if you keep going around
        the questions, the way in which the answers are coming out
        are answering the question.
                 DR. MASSIE:  All right.  
                 What is the appropriate placebo group for this
        comparison?
                 DR. LIPICKY:  And what you have said so far is
        that there isn't any placebo comparison that would be
        appropriate.
                 DR. MASSIE:  And you are happy with that
        answer?  If that isn't an allowable answer, then we should
        have a vote.
                 DR. LIPICKY:  Well, yes.  You can always tell
        us we don't know what we're asking.
                 DR. MASSIE:  Bob?
                 DR. TEMPLE:  Ray is right about needing to get
        on with it, but this is one of the most complicated
        questions in general we face.  What do you do when you
        can't randomize to placebo anymore, which may be is a
        conclusion reached too soon sometimes, but was certainly
        the conclusion reached in this case.
                 In the case of thrombolytics, after some very
        elaborate discussions, anyone who is here will recall 40
        consultants, each giving their opinion about things at
        considerable length.  
                 In a setting where everyone agreed that it
        could be expected that the active control would always beat
        placebo, that conclusion has not been considered here.
                 But in that setting there were rules and
        approaches suggested that were, at least in the opinion of
        the committee then, pretty stringent which included the
        idea that at least 50 percent of the effect of the active
        control should be retained not by point estimate, to my
        best recollection, but as a lower bound conference
        interval, a very stringent criterion, which basically means
        the new drug has to be at least a point estimate better
        than the old one.                                     
                 What is interesting about this case, though, is
        that no one contemplated -- no one clearly thought about
        doing that where the new agent actually is inferior to the
        control agent.  And the question of whether you can really
        ever make a persuasive case in that setting is something
        that bears further discussion.  It's plainly very
        difficult, but you never like to say never.
                 The setting when this was last considered for
        thrombolytics was quite different.  We had four, five
        trials where there was a regular 2 percent or 25 percent
        reduction or whatever, and everybody sort of took that as a
        given, that had there been a placebo, it would have been 2
        percent worse than the control.  The ability to say that
        here seems much more complicated, to say the least.  
                 Now, what is novel here is that Jay has made
        the argument that you have got a relevant group that is
        basically treated the same way.  It is in the same
        environment, and it is rather more plausible than most
        historical controls.  That is not a silly thing to say by
        any means.  The question is whether you believe it.
                 DR. MASSIE:  I think what we are going to do
        because we can't recreate the 40-consultant, 12-hour
        meeting, is to move on to question 11.2, which is, had a
        placebo been present, does this committee think it is
        likely that hydralazine-isosorbide dinitrate would have
        been greater than that of placebo, the effect of.  
                 That seems like a concrete enough thing that we
        could answer, and I guess I heard some discussion and
        sentiment about that already.  So, maybe we can vote.
                 DR. LIPICKY:  To my mind, you have already
        answered that question, if in fact the committee says there
        is no placebo group you can compare the results to.  Then
        you have already answered the question and you don't need
        to.
                 DR. MASSIE:  No.  That was the comment of some
        individual members of the committee.  Do you want us to
        vote or --
                 DR. KONSTAM:  Can I just ask a question?  The
        way you worded this question is different from the way that
        you worded other questions.  You asked, is it likely. 
                 I guess this brings me back to asking you, in
        our own minds, somehow, what level of evidence are you
        asking at each of these points.  I mean, for me, is it
        likely?  The answer would be yes.  Am I convinced?  The
        answer would be overwhelmingly no.
                 DR. LIPICKY:  Right, but I think we need to
        take 15 or 20 minutes to get at that.  And there isn't
        enough time.  So, I would suggest that we skip this
        question in its entirety.  It is getting nowhere.
                 DR. MASSIE:  Okay, sold.
                 Does the mortality of V-HeFT II confirm the
        findings of V-HeFT I?  Do we need to discuss that since we
        --
                 DR. THADANI:  Are we comparing apples and
        oranges?
                 DR. MASSIE:  -- findings of V-HeFT I that were
        significant?
                 DR. RODEN:  I thought we decided that V-HeFT I
        probably didn't show a mortality benefit versus placebo. 
        So, I don't think this is an answerable question either.
                 DR. MASSIE:  Right.  That is what I am asking. 
        Should we answer that question?
                 DR. RODEN:  Well, the answer is no.
                 DR. THADANI:  Barry, didn't you say that since
        there is no placebo and we have two, we can't even talk
        about that?  So, we are comparing apples and oranges while
        we are answering the question.  It's a moot point.
                 DR. MASSIE:  It would seem that question 12 is
        moot.
                 DR. LIPICKY:  It seems fairly straightforward. 
        If you have said that V-HeFT I has no mortality effect,
        then in fact there is no effect to confirm.  
                 DR. MASSIE:  Right.
                 DR. LIPICKY:  And that would be a very simple
        answer.  I think everyone agrees on that.
                 Anyone who doesn't agree on that, raise their
        hand.  
                 (No response.)
                 DR. LIPICKY:  Okay, you're done.
                 DR. COHN:  Is no effect the same as a p value
        greater than .05?
                 DR. TEMPLE:  This is probably a mistake.  The
        committee voted that there was no effect clearly shown in
        V-HeFT I, but when you asked various members what did they
        sort of grunt-believe, there was a sort of a mixed belief
        that there might have been a little something going on.  
                 One possibility is that V-HeFT II supports your
        belief that there's a little something going on because you
        believe the placebo group that has been developed.  
                 Another possibility is that in turning out
        inferior to a drug whose effect is not that large, it
        actually weakens whatever thoughts you had about V-HeFT I.
                 So, I guess I wouldn't insist on a vote, but
        some sense of this may help us figure out how to say or do
        what we say or do.  But if you think that's distracting,
        feel free.
                 DR. MASSIE:  It's getting a little distracting.
                 DR. FENICHEL:  Bob Fenichel, FDA.  Let me see
        if I can sharpen this question.
                 I think it's wrong to reject the question on
        the grounds that, having found no statistically significant
        effect in V-HeFT I, it is intrinsically a non-confirmable
        trial.  
                 Perhaps it's useful to propose a thought
        experiment.  Suppose V-HeFT I had in fact been replicated,
        say, 40 times, and the question were now, do these 40
        replications confirm each other?  
                 Now, if you had held that V-HeFT I was a
        complete waste of time, that it showed nothing, not just in
        a statistical sense, but it didn't give you any sort of
        feeling as to where the truth lay, then the answer plainly
        would be, well, no.  Now you have just done nothing 40
        times.  
                 But the answer might be, well, V-HeFT I trended
        in the right direction and gee, if you saw a trend in the
        right direction 40 independent times, that would be pretty
        impressive.
                 So, it is possible for a study which shows
        nothing by itself to be confirmable or not, and that is
        what this question was trying to draw your attention to.
                 DR. THADANI:  The question said V-HeFT II was
        designed to compare hydralazine with Enalapril has no
        relevance to V-HeFT I.  All you are saying in this
        particular study, Enalapril was superior to hydralazine,
        and there is no way of saying that it replicated the V-HeFT
        I study.  I don't know how you can say that.
                 DR. FENICHEL:  I think that the facts make it
        difficult for me to find confirmation in V-HeFT II of V-HeFT I, but I think that it is an askable question.
                 Suppose it were true that Enalapril is known to
        be immensely better than placebo every time, essentially
        reducing mortality to 0 from 100 percent, and suppose it
        were further true that in V-HeFT II the hydralazine-isosorbide dinitrate combination had been associated with,
        say, 2 percent mortality instead of 100 percent, and it
        were large enough to be distinguishable, surely, from
        Enalapril.                                                 Nevertheless, you might say, gee, that's pretty
        good.  That really does confirm the kind of trend in V-HeFT
        I.  
                 What I am asking you to do, I think there is an
        answerable question.  I think this is not a null question. 
        V-HeFT I is confirmable or disconfirmable on the basis of a
        positive control study.
                 Now, you may believe that it was not in fact
        confirmed by this particular study, but that is a separate
        answer.  I am asking you not to reject the question.
                 DR. MASSIE:  So, you are just asking, could you
        confirm the results --
                 DR. FENICHEL:  No.  I'm asserting that it
        couldn't confirm.  I am saying --
                 DR. LIPICKY:  Maybe the way to put it is, let's
        say that hydralazine-ISDN significantly beat Enalapril and
        you are wondering, did ISDN-hydralazine beat placebo in
        V-HeFT I.  I think you could say V-HeFT II confirms V-HeFT
        I.  It turns out it was the converse.
                 So, the question is addressable, okay.  It is
        really a very simple answer I think, and you were making it
        complicated so I was going to skip it.  
                 DR. MASSIE:  Well, I think that you heard that
        the committee didn't feel you could draw conclusions from
        V-HeFT II about the effect of hydralazine and isosorbide
        dinitrate on mortality.  And therefore, both because there
        was no finding to confirm, and because they couldn't draw
        conclusions, it sounds like we have already answered the
        question.
                 DR. TEMPLE:  Barry?  
                 DR. MASSIE:  Yes.
                 DR. TEMPLE:  Let me try again.  
                 To those people who thought that V-HeFT I might
        have been a good lean, do they feel stronger or less
        strong, having seen the results of V-HeFT II in which the
        drug was inferior to another agent? 
                 DR. MASSIE:  Well, there were four of them,
        according to the vote, and maybe we can just ask them and
        move on.
                 DR. TEMPLE:  Fine.  But I think that is the
        sort of thing we are getting at.  Obviously you can't
        confirm something you didn't believe fully in the first
        place.
                 DR. GRINES:  I was one who thought that the
        mortality figures looked pretty good for V-HeFT I, but I
        would say that if there is a 30 percent reduction in V-HeFT
        I, I would have expected to see some sort of advantage or
        at least equivalence in the second study.
                 To my knowledge, ACE inhibitors don't reduce
        mortality by 50 percent, so I am somewhat surprised that
        isosorbide and hydralazine lost in V-HeFT II.  I would say
        that I am less enthused about the mortality advantage.
                 DR. MASSIE:  Okay.  Anybody else?
                 DR. WEBER:  Yes.  One of the things that was
        impressive to me in the two separate studies, nevertheless
        done by the same bunch of investigators and using very
        comparable patients, was that the survival curves on the
        two studies were virtually superimposable.  In fact, they
        truly were superimposable.
                 So, what happened when you got hydralazine-ISDN
        in the second study was that you finish up pretty much the
        same place as the first study.  So, whatever the first
        study showed, I guess the second study wouldn't weaken my
        belief in the results of the first study.  It wouldn't
        confirm it, but it wouldn't disconfirm it or nonconfirm it
        either.
                 So, as one of the people who originally said I
        thought there was probably something in it, I haven't been
        persuaded to abandon that point of view.
                 DR. MASSIE:  Well, there, Bob, you get two
        sides of the same thing.  Can we move on?
                 Exercise capacity was measured by maximum
        oxygen consumption at peak exercise and total duration of
        maximum exercise.  Results of both measures of exercise
        capacity in both the division's and sponsor's view gave
        similar results.
                 DR. LIPICKY:  Barry, excuse me.  You are
        anticipating the answer you gave several questions back. 
        It was going to be repeated.  But that's okay.  You can
        skip this.  You really have already answered it.  You just
        didn't go through it in the detail we wanted.  So, we know
        your answer to this.  You can go on to 14.
                 DR. MASSIE:  Which was hospitalizations, but as
        I remember, there were no data to support a reduction in
        hospitalizations, I mean, within the same absence of a
        placebo control group.  So, maybe there is not much that we
        need to further do with that.  JoAnn?
                 DR. LINDENFELD:  Right.  There was no
        hospitalization difference.
                 DR. MASSIE:  And now we get to the ejection
        fraction.  Was there a statistically significant treatment
        effect on ejection fraction favoring hydralazine-isosorbide
        dinitrate in V-HeFT II?
                 DR. LINDENFELD:  There was at 3 months but not
        thereafter, so I think overall probably not.
                 DR. MASSIE:  Anybody feel otherwise? 
                 (No response.)  
                 DR. MASSIE:  Is that okay, Ray?
                 DR. LIPICKY:  Yes.
                 DR. MASSIE:  How compelling is the evidence
        that hydralazine prevents the occurrence of tolerance to
        isosorbide dinitrate?  Do you want us to discuss that?
                 DR. LIPICKY:  Yes.  Well, all right, no. 
                 (Laughter.)  
                 DR. LIPICKY:  Skip it.  
                 DR. MASSIE:  I don't think you will get a
        definitive answer out of this committee.
                 DR. KONSTAM:  Can I ask Jay a question about
        this?  You talked about data from your remodeling model
        with nitrates showing benefit without hydralazine.  Isn't
        that right?  How then would you argue that perhaps the
        remodeling endpoint requires the protection from tolerance?
                 DR. COHN:  Well, the data in the animal model
        were done with isosorbide 5-mononitrate given twice daily. 
        We don't suggest for a moment that ISDN by itself on
        remodeling would necessarily induce tolerance.  For those
        who think that it may -- and I think Ray has been very
        concerned about the tolerance issue -- at least we have a
        mechanism by which this combination might inhibit tolerance
        and we don't know in humans, of course, whether the
        tolerance is a major issue or not.  I think all those
        things are true.  
                 I think it's important to point out when we get
        to the ejection fraction data, although that has never
        served as a provable indication for the treatment of heart
        failure, that there is remarkable congruence in all trials
        between the change in ejection fraction and the change in
        mortality.
                 There is in the animal model that I have
        alluded to clear evidence that nitrates and ACE inhibitors
        block remodeling that an alpha blocker equivalent to
        Prazosin that we used in V-HeFT I does not, despite the
        fact that it has a hemodynamic effect.  So, there is
        incredible congruence between mortality effects, long-term
        changes in ejection fraction, and the drugs that one uses.
                 So, although this is not ready yet I think for
        an indication, I think it should be strongly considered as
        clear evidence that a drug is altering the natural history
        of the disease.
                 DR. MASSIE:  What about digoxin?
                 DR. COHN:  We haven't studied digoxin in our
        model.
                 DR. MASSIE:  In your model, but in the human
        it's a drug that increases ejection fraction and seems to
        have a neutral effect on mortality.
                 DR. COHN:  Of course, in the dig trial there
        was no ejection fraction measurement, so we don't know what
        happened in that trial.  The only data we have is up to 6
        months, which may well be in the right direction.  And as
        you know, in the dig trial there was a reduction of pump
        failure deaths, but the drug independently has an adverse
        effect on electrical activity and there was an increase in
        sudden deaths, probably so.  That may well be consistent
        with the other observations.
                 DR. THADANI:  Jay, on that question on ejection
        fraction, inotropes increase ejection fraction, have a
        negative effect on mortality.  There may be a difference
        between the mechanism of increasing ejection fraction or
        vasodilators might be different.
                 DR. COHN:  No, there is no data showing long-term improvement in ejection fraction with any inotropic
        drug other than digoxin, that Barry points out, which we
        have 6-month data for.  But there is no other data.  
                 We have data out to 4 years here with ejection
        fraction, which really is a remodeling phenomenon, not the
        short-term hemodynamic increase in ejection fraction that
        may occur when you give dobutamine or amrinone acutely and
        demonstrate that the heart empties better temporarily, but
        that is not a remodeling issue.
                 DR. THADANI:  Would hydralazine alone do that
        without nitrates?
                 DR. COHN:  We don't know.
                 DR. TEMPLE:  Jay, do you know whether if you
        stop the drug for a couple of weeks, the increased ejection
        fraction persists?
                 DR. COHN:  No, we've never studied that, Bob. 
        That has been studied with the ACE inhibitor.  When one
        stops the drug, the benefit persists so that it isn't all
        hemodynamic.  It's structural.  But we've never done that
        with hydralazine and isosorbide dinitrate.
                 DR. TEMPLE:  That seems a crucial question if
        one wants to believe that there's remodeling and all that
        stuff, to be sure you separate out the hemodynamic effects. 
        But you think it probably would persist?
                 DR. COHN:  Oh, I think a lot of it will because
        it is a structural change.  It's not a hemodynamic change. 
        I think we know very well from a lot of basic studies that
        that is a change in myocyte length and interstitium which
        really would persist when one stops the drug, at least for
        a period of time.
                 DR. CODY:  Of course, the other paradox here is
        that even though the ejection fraction goes up, we can't
        really attach a mechanism to it.  I think people implicitly
        attach that contractility is improved.  The paradox is
        that, to pick up on Udho and Jay's point, positive
        inotropes do not uniformly increase ejection fraction,
        whereas beta-blockers, at least in a number of trials, do. 
        So, if the beta-blocker is increasing the ejection fraction
        is it by positive inotropic effect?
                 DR. MASSIE:  I guess we will hear more about
        this.
                 Okay, the next set of questions I'm not sure is
        relevant at this point, that is, getting into the details
        of the dosing and instructions.
                 DR. LIPICKY:  Fine.  Why don't you just go on
        to --
                 DR. MASSIE:  We could go back to 17.
                 DR. LIPICKY:  Well, go on to the last question. 
        That's fine.
                 DR. MASSIE:  So, I think the last question is,
        should BiDil be approved for use in the treatment of
        congestive heart failure?
                 Again, I guess any discussion.  We'll start
        with JoAnn.
                 DR. LINDENFELD:  I think given all the
        discussion that we're not certain of the benefit, it would
        be hard to recommend it.  So, I would vote no.
                 DR. KONSTAM:  Barry, are we discussing or are
        we voting yet?
                 DR. MASSIE:  Discussing.
                 DR. KONSTAM:  I guess the question that I have
        in my mind is, is there a circumstance where the FDA would
        consider a lower standard for approvability than is normal,
        because in my mind the data clearly do not reach the usual
        level of approvability statistically, or on the basis of a
        clinical judgment of a certain finding, or a clearly
        reproducible finding.
                 I guess the arguments in my mind that perhaps
        the FDA might consider a lower threshold here are some of
        the arguments that Jay made.  This is a study that was done
        a long time ago that cannot be reproduced.  The data trend
        strongly in the right direction.  There is not a
        significant concern about safety.  The finding in favor of
        survival at least tracks with some other things like the
        ejection fraction, which often goes along, and the study
        cannot be reproduced at this point.  
                 For all of those reasons, I think if there were
        a circumstance where the FDA would consider a lower level
        of approvability than the usual, I think this might be one.
                 DR. THADANI:  I think, realizing the study was
        done in 1980 but we learn with experience so we can't say
        what we have learned we are going to ignore and go on the
        evidence or the judgment made in 1980.  
                 One of the worries I have, you are going to
        lower the standard of approvability.  Once you start that,
        there is no end to it and you could talk about any trial we
        do.  You've got six endpoints, four endpoints, one is
        positive, you are going to approve it.  So, I think I've
        got major problems with the previous speaker on that issue.
                 DR. MASSIE:  Well, I don't think -- he was
        asking.
                 DR. TEMPLE:  We're actually actively thinking
        about how much evidence one needs, but there were a couple
        of things that are worth saying.  There isn't any magic p
        value.  There are conventions but we don't sit here and say
        if you're .053, you're toast, or something like that.  It
        doesn't work that way.
                 From time to time, although I don't know if
        everybody would agree, we've actually accepted one-sided
        tests.  The approval of nifedapine for unstable angina was
        done with a one-sided test because we thought we were
        confirming something.  I just thought I'd mention that.  We
        don't usually do it, but that's really a convention.  It's
        not written in stone.  There isn't any law or regulation
        that says the p value shall be .05 two-sided or .025 one-sided.  It's a convention and it represents a strength of
        evidence.  So, that's one thing.  
                 Everybody knows that from time to time we have
        accepted persuasive, unreplicated findings as a basis for
        approval.  That usually involves a clear mortality effect
        and it usually involves very low p values so that they are
        persuasive in one way or another on their own.
                 The discussion has been very interesting.  I
        think, from my point of view, we'd have a rather more
        difficult time if all we had was V-HeFT I because then
        you'd have a marginal -- then everybody would look and say,
        well, it's sort of close and it's mortality and you can't
        do it again and all that.
                 To me it's why I keep pressing this question. 
        The existence of V-HeFT II is, relatively speaking, quite
        damaging because it isn't easy to lose to another active
        drug, if you're active.  Those studies are not very
        sensitive to do that.  
                 So, when you talk about lowering the standard,
        the question is, what does that mean and what do people
        have in mind?
                 There isn't any absolutely rigid standard, as
        anyone who has followed these committee meetings can easily
        deduce.  But there is some sense that you're supposed to
        believe it with a reasonably high level of assurance, and
        we get advisory committees to help us figure out what that
        level of assurance ought to be. 
                 But there isn't a whole lot of credit given
        because it's old, because the study was smaller than it
        would have been if they were really thinking about a
        mortality trial.  Those are just the facts of life and it's
        hard to give credit for that because when it's too small,
        that means you don't really know the answer.  It's not that
        the answer would have been the same but more significant if
        you had done a bigger study.  You don't know that.
                 So, those are just some thoughts.  We are
        actively trying to write down the sorts of things we think
        about when we consider evidence.
                 One thing we definitely can do is think about
        the relevance of pharmacologic activities of short-term
        studies and things like that.  We can do that.  The
        question we will put to advisors is what cases we should do
        that in.
                 DR. MASSIE:  Bob?
                 DR. CODY:  Of course, any decisions along these
        lines today not only affect deliberations for future trials
        but maybe as soon as this afternoon.  So, I think there is
        a difference here.  
                 This is not a new drug or a new drug
        combination.  When I said no for the statistics but yes to
        how it influenced me clinically, back in the 1980s this
        V-HeFT I was the final nail in the coffin for Prazosin. 
        So, I wasn't alone in that decision.  Everybody else in
        heart failure stopped using Prazosin.  So, people voted
        with their guts for V-HeFT I a long time ago.
                 V-HeFT II, I would agree, is sort of a negative
        in the sense that while, yes, the combination was better
        than placebo, but it looks like Enalapril is better than
        this combination.  However, it looks like because of the
        exercise, maybe the combination of Enalapril and
        hydralazine and nitrates would be beneficial.  That remains
        untested.  So, we can't really address that at all.   
                 So, I think what we are looking at is a drug
        combination that we do have a lot of historical information
        about.  We know, as Jay has pointed out, that there has
        been no really serious adverse effect with this combination
        sufficient enough to raise it to everyone's level of
        consciousness.  
                 This has been approved by three guideline
        groups as an effective alternate therapy.  The drug
        combination suggests we put brackets around a totally
        loosely uncontrolled range of drug combinations of
        hydralazine and nitrates that are being used out there.
                 I think that the data that was presented does
        suggest that the combination of hydralazine with the
        nitrates attenuates the adverse effects of nitrate
        tolerance.  
                 So, I don't think we're being asked to really
        necessarily here make with our decision something that's
        going to "lower the standards" for future deliberations,
        even as soon as this afternoon.  So to address Marv's
        question, Dr. Konstam's question, I think this might be a
        case for the reasons that he mentioned and I've mentioned,
        where one might look at this combination differently and,
        at the same time, not lowering the standards for how a new
        drug coming here might be evaluated.
                 DR. MASSIE:  Jeff?
                 DR. BORER:  I think that all the points that
        have been made just now by Bob and by Udho are very
        important, but since the two components are available, and
        since they are usable if someone believes they are
        appropriate to be used, I don't think it's necessary to
        consider changing FDA standards for approvability.  
                 The drugs are there, the literature is there. 
        It's not illegal to put them together in a certain dosage
        form and use them if you believe that's right.  The
        question we're being asked is, are the data supporting that
        use sufficiently consistent and sufficiently reproducible
        so that we can recommend that that should be done as a
        routine procedure by any clinician who wants to do it?
                 I think the answer is, we don't have the degree
        of assurance that would allow us to do that.  Again, if
        somebody disagrees, the drugs are there, the literature is
        there.  One is free to use these drugs in heart failure.
                 The practical impact of the FDA not approving
        this combination today is that there won't be an economic
        incentive for the sponsor to get out and provide
        educational material for a lot of doctors to know how to
        use the drugs best.  I think that is the impact. 
                 DR. CODY:  Just along those lines, one of the
        issues that came up was the need for prescribing
        information.  I think ultimately that's going to be
        addressed best in labeling.  
                 But getting back to our very early discussions
        -- and Barry raised this -- yes, it might be true that only
        40 or 50 percent of patients are receiving ACE inhibitors,
        but that doesn't mean the other 50 percent wouldn't benefit
        from them.  It means that for whatever reason the message
        isn't out there.  So, the use of the term of this as
        alternate therapy might be a little bit misleading in that
        regard.  
                 At the same time, in the labeling we can't say
        anything about whether or not this combination is
        beneficial added to an ACE inhibitor.
                 There are also the minor issues of no data for
        functional class 4 patients and perhaps even a smaller but
        I think timely or at least politically correct point, we
        don't have any information in women.
                 DR. MASSIE:  Well, I think we've had some
        discussion.  I think we need to take a final vote on this. 
        Why don't we start on the right there.  Cynthia, do you
        want to lead off the vote on whether this is approvable or
        should be approved for the treatment of heart failure?
                 DR. GRINES:  No.
                 DR. MASSIE:  Udho?
                 DR. THADANI:  No.
                 DR. MASSIE:  Jeff?
                 DR. BORER:  No.
                 DR. D'AGOSTINO:  No.
                 DR. DiMARCO:  No.
                 DR. MASSIE:  No.
                 DR. LINDENFELD:  No.
                 DR. MOYE:  No.
                 DR. WEBER:  I'm going to vote yes.  I felt that
        there was enough information provided to give me reasonable
        confidence that the drug was beneficial or the product was
        beneficial or would be beneficial in a different
        formulation.
                 I believe that physicians are being encouraged
        to use it by reputable agencies that issue guidelines and
        advice to physicians.  
                 I think the availability of the combination
        would encourage physicians to use hydralazine together with
        the ISDN rather than just the ISDN alone, which I think may
        be important to improve the quality of care.
                 And I do not have the same concern that one or
        two others have expressed about weakening FDA standards.  I
        think FDA standards are absolutely critical when you're
        considering new molecules or new paradigms of treatment or
        some kind of definite new step away for what's currently
        being done or what's currently available.  But here we're
        just finding a way to make more convenient, and I think
        more efficacious a treatment that's already in use, and I
        can't see any real down side to approving it.  
                 So, that's why I would vote yes.
                 DR. RAEHL:  I think the totality of the
        evidence supports approval of this drug.  However, I would
        say that when we think about labeling that it would be
        adjunctive to dig and diuretics in the treatment of chronic
        heart failure in particularly those patients who have
        sensitivity or demonstrated intolerance to an ACE
        inhibitor.
                 DR. KONSTAM:  I guess I would give the FDA my
        clear view that this does not meet its usual criteria for
        acceptability.  I think that's very clear to me.  I would
        still vote yes, approval, because I think perhaps this fits
        into a circumstance that I might lower that standard
        without, as Mike points out, influencing future decisions.
                 DR. RODEN:  No.
                 DR. MASSIE:  Well, I think that we've gotten
        through the agenda, and it's one minute before the
        scheduled time.  So, we should get together by 10 after
        2:00.  That's 40 minutes, and get the discussion started
        shortly thereafter.
                 (Whereupon, at 1:29 p.m., the committee was
        recessed, to reconvene at 2:15 p.m., this same day.)
        
        
        
        
        
        
        
        
        
        
        
                     AFTERNOON SESSION
                                                (2:21 p.m.)
                 DR. DiMARCO:  This afternoon we will be
        discussing NDA 20-297, Coreg, or carvedilol, for the
        indication of congestive heart failure.  The first part of
        the presentation will be the sponsor's presentation.  If
        they would like to start, they are free to do so.
                 DR. POWELL:  Thank you.  Dr. Temple, Dr.
        DiMarco, Dr. Lipicky, members of the Cardiorenal Advisory
        Committee, good afternoon.  My name is Bob Powell.  I'm
        Vice President for Regulatory Affairs at SmithKline Beecham
        Pharmaceuticals.  
                 We at SmithKline Beecham and Boehringer
        Mannheim appreciate this opportunity to present the
        information on the use of carvedilol, Coreg, for the
        treatment of congestive heart failure.
                 As you know, this meeting represents the second
        time that the committee has been asked to review carvedilol
        for the treatment of congestive heart failure.  For those
        of you who were present in May, you will recall that at
        that time the committee and the FDA agreed that carvedilol
        SNDA contains one study, study 240, that provides
        information that would support the approval of carvedilol
        for heart failure.
                 However, while the results of several other
        trials were presented at that time, and most of these
        trials showed favorable effects of carvedilol in a variety
        of prespecified clinically important measures of efficacy,
        many of these measures were secondary endpoints in trials
        that did not achieve statistical significance for their
        primary endpoint --
                 DR. DiMARCO:  Excuse me, Dr. Powell.  Can we
        dim the lights for the front so the slides project better?
                 DR. POWELL:  -- in trials that did not achieve
        statistical significance for their primary endpoint,
        notably improvement in exercise tolerance.  
                 Also, the final report from a major study,
        study 223, performed in Australia and New Zealand, had not
        been submitted to the FDA prior to that meeting and thus
        the committee was unable to fully assess the value of study
        223 at that time.  The committee by a vote of 4 to 2 did
        not recommend approval of Coreg.
                 Finally, I should add that neither the
        committee nor FDA raised any significant safety concerns
        about the use of carvedilol for the treatment of CHF.
                 Since the May meeting, we have submitted and
        FDA has reviewed three types of new information.  
                 First, we submitted the final report of the
        long-term results of our second major trial, study 223,
        which we believe confirms the effects seen in study 240.
                 Second, in response to specific requests from
        FDA, we submitted additional analyses of the effects of
        carvedilol on morbidity and mortality, as observed in
        previously reported multi-center trials, studies 240, 221,
        and 220.
                 And third, we have provided additional
        information to clarify the effect of carvedilol on CHF
        symptoms and clinical status.  I am pleased to note that we
        have reached full agreement with the FDA on the data, the
        analyses, and the nominal p values associated with the
        carvedilol database that are summarized in your briefing
        document.  What remains, however, is to reach agreement on
        the proper interpretation of these data and analyses.
                 As part of the meeting, you will be asked
        several questions concerning the efficacy of Coreg, all of
        which lead ultimately to the single question, should Coreg
        be approved for the treatment of congestive heart failure.
                 In examining this question, we wish to
        emphasize that there is a hierarchy of drug effects that
        should be considered in deciding if Coreg demonstrates a
        clinically important effect in the treatment of congestive
        heart failure.  In any hierarchy of benefits, mortality
        would be the most important.  Second would be effects on
        morbidity, followed by effects on clinical symptoms and
        status, and finally, effects on hemodynamics.  
                 While we are not seeking a survival claim per
        se for Coreg, it is of note that in the U.S. multi-center
        trial program treatment with carvedilol was associated with
        a 65 percent decrease in the risk of death, with the
        nominal p value of 0.0001.  While this observation led to
        the Data and Safety Monitoring Board's recommendation to
        terminate the entire program and offer carvedilol to
        patients taking placebo, we understand that there can be a
        legitimate debate about the appropriate regulatory course
        of action for a survival claim based on data from trials
        not specifically designed to detect a mortality benefit.
                 Nevertheless, this finding does effectively
        rule out the possibility that carvedilol has an adverse
        effect on survival. 
                 A directionally positive but not statistically
        significant effect on mortality was also observed in study
        223, and the overall mortality benefit based on all
        placebo-controlled trials with carvedilol suggests a
        relative risk of 0.51, and an overall nominal p value of
        0.001.
                 In our hierarchy of effects, after a reduction
        in mortality, evidence of a reduction in the worsening of
        CHF would clearly be an important benefit.  In all of our
        multi-center trials, we prospectively monitored
        hospitalization as a measure of worsening CHF.  You will
        find that it is the data on hospitalizations, or more
        specifically, the combined endpoint of hospitalization or
        death, that are most convincing that Coreg produces a
        clinical benefit in these patients.
                 Why the combined endpoint?  In fact, the
        combined endpoint is clearly a better measure of worsening
        of CHF than hospitalization alone because death is in fact
        simply the worst possible outcome.  If, for example, all
        patients in one group had been hospitalized and all
        patients in the other group had died, the conclusion would
        not be that the deceased group was better off.
                 Thus, we believe that mortality is an
        appropriate and necessary part of the measure of morbidity. 
        We will provide prospective data from two well-controlled
        trials and retrospective analyses of data from two
        additional trials that demonstrate a positive effect on the
        combined endpoint of morbidity and mortality.
                 The third benefit of Coreg in our benefit
        hierarchy is the effect of Coreg on the clinical symptoms
        and status.  Data from eight placebo-controlled trials show
        that Coreg produced consistently favorable effects on each
        of several measures of symptoms in clinical status within
        and across studies, including New York Heart Association
        class, CHF symptoms, and global assessments.
                 In addition, to complete our hierarchical
        profile, Coreg produced consistently favorable effects on
        left ventricular ejection fraction measured noninvasively,
        as well as left ventricular function assessed invasively. 
        Thus, Coreg produces a variety of favorable effects across
        the entire hierarchy of desirable outcomes for patients
        with CHF.
                 However, there is considerable variability with
        respect to the ability to demonstrate any one of these
        effects in any given clinical study.  This raises an
        important question.  How variable are the outcomes of
        clinical trials of compounds recognized to be useful in
        CHF?
                 In response to a request by Dr. Temple, Dr.
        Milton Packer has reviewed the data from the NDAs of all
        five drugs approved for CHF during the last decade.  He
        found that there was no measure that distinguishes drug
        from placebo in all trials for any given compound, and that
        clinical symptoms were significantly improved compared to
        placebo in only about half of the trials in which they were
        measured.
                 Further, despite the fact that fewer than 50
        percent of the trials conducted with these drugs reached
        their primary endpoint, it was possible to assess their
        effectiveness on the basis of concordance of findings
        across trials, including those which failed to reach the
        protocol-defined primary endpoint.
                 In our presentation today, we will provide
        evidence from two well-controlled trials that demonstrate a
        reduction in morbidity and mortality, as well as a
        concordance of data demonstrating positive effects on
        clinical symptoms and status, in addition to favorable
        effects on hemodynamics.  We believe that these data meet
        the usual standard used to assess drugs for the treatment
        of CHF.  In fact, based on this database, Coreg is now
        available in several countries outside the U.S. for the
        treatment of CHF.
                 Having said that, we recognize that the
        carvedilol database does have some limitations, and we
        would propose that these can be adequately handled in
        labeling.  For example, we believe that one limitation of
        the current file is the lack of any extensive clinical
        experience in patients with class IV heart failure. 
        Therefore, we are not at this time recommending that
        carvedilol be used to treat patients with CHF symptoms at
        rest, particularly those hospitalized for worsening heart
        failure or receiving intravenous medications for heart
        failure.
                 One final comment.  In the FDA medical and
        statistical review, it is noted that carvedilol is, after
        all, currently approved in the U.S. for hypertension, and
        it is suggested that since carvedilol could be available
        for the treatment of hypertension, there is no compelling
        need to approve carvedilol for CHF at this time, suggesting
        that physicians would be free to use the drug, off label,
        for CHF based on peer-reviewed publications that have
        appeared in the New England Journal of Medicine,
        Circulation, and most recently, The Lancet, describing the
        clinical program for carvedilol in CHF.
                 We would take exception to this view,
        particularly for a drug like carvedilol.  Initiation of
        therapy with carvedilol in CHF requires considerable
        caution and can be best achieved only if the prescribing
        physician has substantial knowledge about the associated
        risks and their management.  It is the need for careful
        titration and a desire to provide the appropriate
        information to the physician that has resulted in our
        decision not to launch carvedilol for hypertension, despite
        its approval for that indication some 17 months ago.
                 We believe that the proper physician education
        cannot be readily achieved under current FDA regulations
        without an approved claim for the treatment of CHF, and we
        are accordingly strongly committed to accomplish this
        educational task if the drug is approved.
                 With this background, Dr. Neil Shusterman, Vice
        President of Cardiovascular Clinical Research, SmithKline
        Beecham Pharmaceuticals, will now present the following
        information:  a very brief review of the pharmacologic
        profile of Coreg, a description of its hemodynamic effects,
        and more detailed review of the principal benefits of
        Coreg, its effect on morbidity and mortality, followed by a
        review of its beneficial effects on clinical symptoms and
        status.  He will finish with brief comments on the safety
        and tolerability and come concluding remarks.  
                 Dr. Shusterman?
                 I might point out, as Neil walks up, all the
        slides are numbered in the lower right-hand corner and can
        be retrieved by number if you have any questions, comments,
        or wish a more in-depth discussion following Neil's
        presentation.  
                 DR. SHUSTERMAN:  Thank you, Dr. Powell.  Dr.
        Temple, Dr. Lipicky, members of the Cardiovascular and
        Renal Drugs Advisory Committee, ladies and gentlemen. 
                 I would like to begin by briefly reviewing the
        pharmacologic properties of carvedilol, which may
        contribute to its efficacy in the treatment of heart
        failure.  The drug is a nonselective beta receptor
        antagonist and a selective alpha-1 receptor antagonist,
        with no agonist actions at either receptor.
                 In addition, unlike other beta-blockers, the
        drug exerts antioxidant and anti-proliferative effects. 
        These occur in concentrations similar to those that act on
        adrenergic receptors and produce a variety of benefits in
        experimental models of myocardial and vascular injury. 
        However, the importance of these additional properties to
        the efficacy of the drug in heart failure remains unknown.
                 The actions of carvedilol on alpha and beta
        receptors are responsible for the hemodynamics of the drug
        in patients with heart failure.  The first doses of
        carvedilol produced alpha blockade, resulting in peripheral
        vasodilatation.  As a result, blood pressure falls
        slightly, but cardiac function is usually maintained.
                 During long-term treatment, carvedilol, like
        other beta-blockers, improves cardiac performance as
        reflected by the increases in stroke volume and decreases
        in right and left ventricular filling pressures.  The drug
        produces consistent decreases in pulmonary artery pressures
        and heart rate, but with little effect in the long term on
        systemic blood pressure.
                 In summary, the hemodynamic effects of first
        doses of carvedilol appear to be primarily related to the
        actions on alpha receptors, whereas the hemodynamic effects
        of long-term treatment with carvedilol are related to its
        actions on beta receptors.
                 The ability of carvedilol to improve cardiac
        function has been confirmed in each of the placebo
        controlled trials that have been carried out with the drug. 
        In all, eight studies, therapy when carvedilol, when added
        to conventional therapy for 4 to 12 months produced a 5 to
        9 ejection fraction unit increase in the left ventricular
        ejection fraction, associated with the p values shown here. 
        This increase in ejection fraction with chronic treatment
        is greater than that reported for any other drug evaluated
        for the treatment of heart failure.
                 The improvement in ejection fraction with
        carvedilol was related to the dose of the drug.  In a
        parallel dose response study that compared a low dose, an
        intermediate dose, and a high dose, carvedilol produced
        dose-dependent increases in ejection fraction after 6
        months of treatment.  The p value for this dose response
        was 0.008.
                 This improvement in ejection fraction was
        associated with a decrease in the chamber dimensions of the
        left ventricle.  This decrease in dimensions occurred in
        addition to any effect that an ACE inhibitor might have to
        diminish left ventricular size.  
                 In this placebo-controlled long-term study of
        carvedilol in patients already receiving an ACE inhibitor,
        left ventricular end diastoic and end systolic dimensions
        were measured at baseline, and then after 6 and 12 months
        of treatment.  Whereas both dimensions remained stable over
        time with the placebo treatment, these decreased over time
        with treatment with carvedilol.  The p values for the
        differences between the two groups for both measurements at
        the two time points ranged from 0.0004 to 0.047.  
                 I would now like to describe the clinical
        trials development program for carvedilol in heart failure. 
        Carvedilol has been evaluated, as I said, in eight
        randomized, double-blind, placebo-controlled trials.  These
        studies can be grouped into two categories.  
                 First, the single-center studies, study 033,
        BMI-O1, and 035, each of which enrolled approximately 40 to
        60 patients and maintained double-blind therapy for
        approximately 4 months.
                 The U.S. multi-center program, consisting of
        four studies, 239, 221, 220, and 240.  These studies
        recruited several hundred patients and lasted approximately
        6.5 to as long as 15 months.  
                 And study 223, the Australia-New Zealand heart
        failure trial, which was the largest and longest of the
        trials with double-blind treatment lasting outwards to 18
        to 24 months.
                 Now, the designs of the single-center trials
        are described on this slide.  Each of the three trials
        enrolled patients with a ventricular ejection fraction less
        than or equal to 35 percent.  With persistent symptoms of
        heart failure despite treatment with digitalis, diuretics,
        and an ACE inhibitor, study 033 enrolled patients with mild
        heart failure, while study BMI-01 enrolled patients with
        more moderate heart failure, and study 035 enrolled
        patients with severe heart failure.
                 Again, patients were randomized to either
        carvedilol or placebo for a treatment period of 4 months at
        the target doses indicated here.
                 The design of the U.S. multi-center program is
        shown on this slide.  In this program patients with heart
        failure and an ejection fraction less than or equal to 35
        percent, despite conventional therapy, again with
        digitalis, diuretics, and an ACE inhibitor, entered a
        common screening period, during which an evaluation of
        exercise performance by a 6-minute walk test was performed.
                 Based on the performance on this test, patients
        were then stratified into one of four individual trials. 
        Patients with preserved exercise tolerance were stratified
        to study 240.  Those with intermediate exercise tolerance
        went to either study 221 or 220, and those with the most
        impaired exercise tolerance were assigned to study 239.
                 In all studies, after an open-label period,
        during which patients received low doses of carvedilol to
        determine tolerability, patients were then randomized to
        placebo or carvedilol, up-titrated to target doses over a
        period of 2 to 8 weeks, and then were continued on double-blind therapy during a maintenance period lasting from 6 to
        12 months.  During this time, background medications were
        to be kept constant.  
                 Please note that the allocation ratios to
        carvedilol or placebo varied in the four studies from 1 to
        1, to 3 to 1.  In three of the studies, 240, 221, and 239,
        carvedilol was titrated to a target dose in the range of 25
        to 50 milligrams twice daily, whereas one trial, study 220,
        was designed as a parallel dose-response study with
        patients being randomized to placebo or one of three doses
        of carvedilol.
                 The occurrence of major fatal and non-fatal
        events within each study and across the entire program was
        prospectively monitored by a data and safety monitoring
        board, which recommended early termination of the entire
        U.S. program because of the finding of a favorable effect
        of carvedilol on mortality.  Early termination of the U.S.
        program modestly affected follow-up and recruitment in
        study 240, but had a pronounced effect on both enrollment
        and follow-up in study 239.
                 Finally, the Australia-New Zealand trial was a
        multi-center study which enrolled patients with heart
        failure due to ischemic heart disease.  Again, following
        baseline evaluation, patients with an ejection fraction
        less than 45 percent receiving a diuretic and an ACE
        inhibitor, were randomized to either placebo or carvedilol.
                 This study had two phases.  The short-term
        phase was designed to evaluate several physiologic and
        clinical endpoints at 6 and 12 months, whereas the
        objective of the long-term phase was to evaluate the effect
        of carvedilol on morbidity and mortality over 18 to 24
        months.
                 I would like to begin the discussion of the
        clinical efficacy of carvedilol with a review of the
        effects of the drug on morbidity and mortality.  There are
        two reasons to do so.  
                 First, the effect of any drug on morbidity and
        mortality is of unquestioned clinical importance.  
                 Second, all of the new information and analyses
        that have been performed since the May 1996 meeting of the
        advisory committee have focused on the effects of
        carvedilol on morbidity and mortality.
                 When the clinical trials program with
        carvedilol was being designed, there were good reasons to
        think that the drug could have a favorable impact on the
        natural history of heart failure.  In experimental models
        of heart failure, long-term beta blockade can prevent the
        progression of heart failure when initiated early and can
        reverse the process of ventricular remodeling when started
        later.
                 Beta blockade has been shown to prolong
        survival in cardiomyopathic hamsters also.  
                 And furthermore, long-term treatment with beta
        blockade has been shown to reduce the combined risk of
        morbidity and mortality in large-scale trials with
        metoprolol and with bisoprolol.
                 Evidence that carvedilol could reduce morbidity
        and mortality emerged from the early single-center studies
        with the drug.  One of the single-center studies enrolled
        high risk patients and in this study the investigators
        performed a retrospective analysis of the effect of
        treatment on major cardiovascular endpoints.  
                 Morbidity and mortality was defined as death,
        plus hospitalization for worsening heart failure, or
        resuscitated sudden death.  The combined risk of morbidity
        and mortality was significantly reduced in the carvedilol
        group, p equals 0.028.
                 Thus, based on the experimental data,
        information from trials with other beta blockers, and the
        results of carvedilol in the study just described, the
        hypothesis that carvedilol had a favorable effect on
        morbidity and mortality was developed and then
        prospectively evaluated in the two largest placebo-controlled trials carried out with the drug, study 240 and
        220.  These two trials also had the longest duration of
        follow-up.  
                 First, I will describe study 240.  This slide
        shows its design, which is typical for all of the studies
        in the carvedilol program.  After an initial screening
        period, all patients received open-label therapy with low
        doses of carvedilol for 2 to 3 weeks.  Those who tolerated
        6.25 milligrams twice daily were then randomized to
        carvedilol or placebo in a 2 to 1 ratio.
                 The double-blind period consisted first of an
        up-titration period where patients were increased to the
        target dose, and after that by a 12-month maintenance
        period, during which background therapy was to be kept
        constant.
                 Of the 389 patients who entered the run-in
        period of study 240, 23 did not complete for the reasons
        shown at the top of this slide.  As a result, 366 patients
        were randomized, 134 to placebo, 232 to carvedilol.  The
        two groups were balanced with respect to baseline,
        demographic, and clinical characteristics.
                 During double-blind therapy, approximately 10
        percent of placebo patients but only 7 percent of
        carvedilol patients failed to complete double-blind therapy
        or were active at the time of DSMB decision to terminate
        the U.S. program.  The most important reasons for
        withdrawal were death and worsening heart failure, and
        these events occurred more frequently in the placebo group
        than in the carvedilol group.
                 The primary endpoint for study 240 specified in
        the original protocol was the combined risk of morbidity
        and mortality.  This was prospectively defined as the
        composite of three events:  first, death due to heart
        failure, or sudden death; second, hospitalization for
        worsening heart failure; and third, worsening heart failure
        that was severe enough to require a sustained increase in
        background medication as defined on this slide.
                 Several physiologic and clinical measures were
        prospectively defined as secondary endpoints in this trial,
        and these will be discussed a little later in this
        presentation.  
                 It should be noted that the FDA medical
        statistical review refers to incomplete data on study
        medication in this trial, including a reference to missing
        data on 60 percent of patients.  While study medication
        data have always been complete since the submission of the
        NDA, prior to May 2nd, 1996, the data were not in an easily
        extractable form for computer analysis.
                 On that date, SmithKline Beecham delivered new
        data sets and programs to the FDA that allowed for complete
        electronic replication of our results.  Again, I want to
        emphasize that no medication data are missing on any of the
        patients.  
                 This slide shows the effect of carvedilol on
        the primary endpoint of study 240.  When all randomized
        patients were included in the analysis, 21 percent of the
        placebo group, but only 11 percent of the carvedilol group
        experienced one or more of the three events that comprised
        the primary endpoint.  This difference reflected a 48
        percent reduction in relative risk, significant p value of
        0.008.
                 This slide also shows the breakdown of the
        three events in hierarchical order, with death taking
        precedence over hospitalization, which took precedence over
        a change in CHF medications.  As can be seen, each
        component of the primary endpoint occurred less frequently
        on carvedilol than on placebo.
                 The same data as shown on the previous slide
        are displayed here as Kaplan-Meier plots using a time-to-first-event analysis.  As can be seen, the curves diverge
        early and continue to separate over time.  Placebo is
        indicated in blue-green and carvedilol in yellow.  Using
        this analytic approach, carvedilol reduced the combined
        risk of morbidity and mortality by 53 percent, with a p
        value of 0.005.
                 To further evaluate whether the effect on the
        combined endpoint was related to a concordant effect on its
        individual components, the hierarchical analysis was
        repeated twice after sequentially omitting the least
        important components.  This was done in response to a
        specific FDA request, and these additional analyses were
        submitted by the sponsor to the FDA since the first
        advisory committee meeting on carvedilol.
                 The top line shows the primary endpoint as
        defined in the protocol, and as I showed on the previous
        slides.  The second line shows the effect of carvedilol on
        death and hospitalization.  This analysis was carried out
        by omitting the medication component.  Please note that the
        risk reduction remains stable and the treatment effect
        remains significant.
                 This third line shows the effect of carvedilol
        on heart failure deaths.  This analysis was carried out by
        omitting any contribution of either hospitalizations or
        background medications.  Even when more than 90 percent of
        the events are eliminated, the effect of carvedilol
        remained significant.
                 The analyses on this slide demonstrate that the
        benefit of carvedilol on the primary endpoint in study 240
        does not depend on the medication component.  These results
        and their supportive analyses demonstrate that when added
        to conventional therapy for up to 15 months, carvedilol
        reduces the combined risk of morbidity and mortality in
        patients with chronic heart failure.
                 Next I want to review the results of study 223,
        which was the second large-scale trial that prospectively
        evaluated the effect of carvedilol on morbidity and
        mortality.  Again, this slide shows the study design and as
        in study 240, after an initial screening period, patients
        received low doses of carvedilol and those who were able to
        tolerate 6.25 milligrams twice a day were then randomized
        in a 1-to-1 fashion to either carvedilol or placebo.
                 This was then up-titrated during the first 2
        weeks of the study until target doses were reached, and
        after that, patients were continued on double-blind therapy
        for a maintenance phase that extended for 18 to 24 months.
                 Please remember that the study was divided into
        two phases, a short-term phase, which was designed to
        evaluate the effects of carvedilol on exercise tolerance,
        ejection fraction, and left ventricular dimensions, and the
        long-term phase, which was designed to evaluate the effect
        of the drug on the combined risk of morbidity and
        mortality.
                 A total of 415 patients were randomized into
        the study, 208 to placebo, 207 to carvedilol.  The two
        groups were well matched for most baseline characteristics,
        except for nominally significant differences for sex, New
        York Heart Association class, and history of angina.
                 This study was an investigator-initiated study. 
        The original protocol was written by the investigators, and
        it did not clearly define primary or secondary endpoints. 
        However, the protocol defined specific objectives for the
        two distinct phases of the study.
                 First, it defined the objectives of the short-term phase.  "Data on exercise capacity, left ventricular
        function, and left ventricular size will be collected at
        baseline, and after 6 and 12 months of follow-up."
                 Next, it defined the objectives for the long-term phase.  "Data on mortality and major morbidity,
        including hospitalization for worsening CHF, and signs and
        symptoms of heart failure will be collected over 18 months
        of follow-up in all patients."  
                 The two phases were quite distinct.  The short-term objectives were not evaluated during the long-term
        phase, and the long-term objectives were not analyzed
        during the short-term phase.
                 Carvedilol exerted a favorable effect on two of
        the three short-term objectives, specifically on left
        ventricular ejection fraction and on left ventricular
        dimensions, but it had no effect on maximal exercise
        tolerance.
                 Now, I want to focus the remainder of this
        discussion on mortality and major morbidity in this study,
        and in so doing, I want to emphasize that this information
        has been analyzed and submitted by the sponsor to the FDA
        since the first advisory committee meeting on carvedilol.
                 Mortality and major morbidity was defined by
        the investigators as the main objective of the long-term
        phase of the study.  This was not only noted in the
        original protocol, but it was specifically reiterated in
        writing by the investigators following the completion of
        the short-term phase.
                 Before the blind of the study was broken,
        mortality and major morbidity was operationally defined as
        the combined risk of all-cause mortality and all
        hospitalizations.  This was to be analyzed by a time-to-first-event approach, using a log-rank test.  Morbidity and
        mortality was monitored during the trial by a prospectively
        constituted data and safety monitoring board.
                 All patients in this study were to be followed
        for the intended duration of double-blind therapy.  No
        patient was lost to follow-up for the analysis of
        mortality.  And in addition, no patients were lost to
        follow-up for the analysis of hospitalizations.  This slide
        was an earlier version, and the reason for that is we have
        now obtained complete follow-up information on
        hospitalizations until the end of this study in all 7
        patients.  An analysis you will see today, hopefully,
        reflects the inclusion of these new data.
                 At the end of the trial, 80 to 85 percent of
        the patients at risk were still taking double-blind
        medication and this proportion was similar in the placebo
        and carvedilol groups.
                 This slide shows the effect of carvedilol on
        all-cause mortality and all hospitalizations.  As can be
        seen, the curve diverged after about 6 to 7 months and
        continued to separate over time.  Overall, carvedilol
        reduced the combined risk of morbidity and mortality by 23
        percent, p equals 0.045.  
                 This slide shows the effect of carvedilol on
        the individual components of the combined endpoint.  The
        effect on mortality alone and the effect on morbidity alone
        are concordant with the overall effect on the combined
        endpoint.  
                 Although not specified in the original
        protocol, the FDA requested that the effects of carvedilol
        on morbidity and mortality in study 223 be adjusted for
        baseline covariates to account for the potential imbalances
        in the two groups at baseline.  To do so, three covariates
        of prognostic significance were selected:  NYHA class,
        maximal exercise tolerance, and ejection fraction.
                 When any combination of these three variables
        were included as covariates in a Cox regression model, the
        magnitude of the risk reduction with carvedilol remained
        extremely stable and the effect of carvedilol remained
        significant.
                 To summarize at this point, the effect of
        carvedilol on morbidity and mortality was prospectively
        defined and evaluated in two studies, study 240 and study
        223.  In both studies carvedilol produced an important
        effect to reduce the combined risk of morbidity and
        mortality, over a follow-up period as long as 18 to 24
        months.
                 In order to further substantiate this effect,
        the FDA requested additional retrospective analyses of the
        other large multi-center studies, that is, studies 221 and
        220, recognizing that study 239 was too small and too brief
        to produce meaningful results.  Both studies 221 and 220
        were designed to evaluate the effect of carvedilol in
        patients with moderate to severe heart failure and had
        virtually identical study protocols.
                 Very quickly, this slide shows the design for
        study 221 and you will notice it is identical to study 240,
        except that patients were randomized 1 to 1 to carvedilol
        or placebo, and the maintenance phase was 6 months rather
        than 12 months.
                 Of the 301 patients who entered the run-in this
        study, 23 did not complete, for the reasons shown up here,
        and therefore, 278 patients were randomized to placebo or
        carvedilol, 145 to placebo, 133 to carvedilol, and the two
        treatment groups were balanced with respect to baseline and
        clinical demographic characteristics.
                 During double-blind therapy, almost 21 percent
        of the placebo patients, but 14 percent of the carvedilol
        group, failed to complete double-blind therapy.  All
        reasons for withdrawal, including withdrawals for death and
        worsening CHF, were more frequent in the placebo group than
        in the carvedilol group.
                 The primary endpoint for study 221 was exercise
        tolerance.  Several assessments of symptoms and clinical
        status were specified as secondary endpoints.  One of the
        prespecified secondary endpoints was morbidity, which was
        defined in the protocol as hospitalization for
        cardiovascular reasons.  In addition, mortality was also
        specified in the original protocol as a safety objective
        and was prospectively monitored by an independent
        committee. 
                 This slide shows the effect of carvedilol on
        these prespecified analyses.  When analyzed according to
        the original protocol, carvedilol reduced the risk of
        cardiovascular hospitalization by 46 percent and the risk
        of death by 43 percent.  
                 Although the effect on morbidity alone was
        nominally significant, one needs to be very careful about
        looking at morbidity alone.  Since patients with the most
        rapid or severe deterioration die before being
        hospitalized, an analysis of morbidity alone excludes
        patients with the worst outcome.  
                 For these reasons, the FDA asked the sponsor to
        perform an analysis of the combined risk of morbidity and
        mortality.  To ensure the robustness of these analyses,
        three definitions were used:  first, the combination of
        morbidity alone and mortality alone as defined in the
        original protocol for study 221; second, the combined risk
        of morbidity and mortality as defined in study 240; and
        third, the combination of morbidity and mortality as
        defined in study 223.
                 This slide shows the effects of carvedilol on
        the combined risk of morbidity and mortality, using these
        three definitions.  As can be seen, depending on the
        definition used, the combined risk of morbidity and
        mortality was reduced by 39 to 43 percent with carvedilol. 
        With the study 240 definition, the p value was 0.004.  With
        the study 221 definition, the p value was 0.029, and with
        the study 223 definition, the p value was 0.019.
                 This slide shows the Kaplan-Meier curves for
        the effect of carvedilol on the combined risk of death or
        hospitalization for any reason.  This analysis is being
        shown graphically because it was the definition used in the
        study 223 and it makes the fewest assumptions about the
        specific cause of an event.
                 As can be seen, the curves diverged early and
        continued to separate during the entire duration of follow-up.  Overall carvedilol reduced the combined risk by 39
        percent, p equals 0.019.
                 Next, let us take a look at study 220, the
        second study in patients with moderate to severe heart
        failure.  Shown here again is the design, and again, it is
        identical to study 221, except now patients are randomized
        to one of three doses of carvedilol rather than to a single
        dose.  Otherwise, the two protocols were identical.
                 Of the 376 patients who entered the run-in, 31
        did not complete for the reasons shown up here, leaving 345
        patients to be randomized to the groups as shown below. 
        The four groups were balanced with respect to baseline
        clinical and demographic characteristics.  
                 During double-blind therapy, 25 percent of the
        placebo group but only 8 to 17 percent of patients
        randomized to carvedilol failed to complete double-blind
        therapy.  The p value for the relation between dose and
        completion rate was 0.008.
                 Again, as in the case of study 221, the primary
        endpoint for this study was exercise tolerance.  Several
        assessments of symptoms and clinical status were specified
        as secondary endpoints.  One of those prespecified
        secondary endpoints was morbidity, defined in the same way,
        that is, hospitalization for cardiovascular reasons.  And
        mortality was also prespecified as a safety objective for
        the study.
                 This slide shows the effect of carvedilol on
        these prespecified analyses.  When analyzed according to
        the original protocol, the risk of cardiovascular
        hospitalization was reduced by carvedilol by 45 percent,
        and the risk of death was reduced by 73 percent, with the p
        value shown here.
                 However, as stated earlier, we should be
        careful in looking at morbidity alone because patients with
        the most rapid or severe deterioration died before being
        hospitalized, and an analysis of morbidity alone therefore
        excludes patients with the worst outcome.
                 For these reasons again, we were requested to
        perform an analysis on the combined risk by the FDA and to
        ensure the robustness of those analyses, we performed them
        in the exact same three ways as of study 221.  That is, the
        combination of morbidity alone and mortality alone as
        defined in the original protocol for study 220, the
        combination of morbidity and mortality from study 240, and
        the combination of morbidity and mortality from the
        Australian-New Zealand trial, study 223.
                 This slide shows the effect of carvedilol on
        the combined risk of morbidity and mortality using these
        three definitions.  For all of these analyses, please note
        that the effect in the three carvedilol groups has been
        combined into a single group.  As can be seen, depending
        upon the definition used, the combined risk was reduced by
        carvedilol from 32 percent to some 54 percent.  When the
        study 240 definition was used, the p value was .049.  Using
        the study 220 definition, the p value was .001, and using
        the study 223 definition, the p value was .002.
                 This slide shows the Kaplan-Meier curves for
        the effect of carvedilol on the combined risk of death or
        hospitalization for any reason.  Again, this is being shown
        because it was the definition used in 223 and uses the
        fewest assumptions in assigning the cause for an event. 
        Again, the curves diverged early, remained separated
        throughout the follow-up period, and the overall reduction
        in the combined risk was 49 percent, with a p value of
        0.002.
                 This slide and the two that follow summarize
        the effect of carvedilol on morbidity and mortality in the
        major multi-center trials.  This slide shows the effect of
        carvedilol on the combined risk of worsening heart failure,
        leading to death, hospitalization, or a need for increased
        medications.  Please recall that this was the definition of
        morbidity and mortality and the primary endpoint in study
        240. 
                 For all three studies, the relative risks are
        less than 1, and there is considerable overlap of the
        confidence intervals, none of which include unity.  When
        the studies were combined to estimate overall treatment
        effect, carvedilol reduced the combined risk of morbidity
        and mortality by 40 percent, p equals 0.0001.
                 This slide summarizes the effect of carvedilol
        on the combined risk of death or hospitalization due to any
        cause, and again, this was the definition of morbidity and
        mortality from the long-term phase of study 223.  For all
        four studies, the relative risks are less than 1, and there
        is substantial overlap of the confidence intervals.  When
        the studies were combined to estimate an overall treatment
        effect, carvedilol reduced the combined risk of morbidity
        and mortality by 31 percent, again with a p value of
        0.0001.
                 Finally, this slide summarizes the effect of
        carvedilol on the combined risk of death or cardiovascular
        hospitalization.  This was the definition of combined risk
        based on the prespecified definition of morbidity alone and
        the prespecified safety objective of mortality alone in
        studies 221 and 220.  Again, for all four studies, the
        relative risks are below 1, the confidence intervals
        overlap, and when the studies were combined, an overall
        estimate of the treatment effect showed by carvedilol
        reduced the combined risk by 35 percent, with a p value of
        0.0001.
                 In summary, carvedilol reduced the combined
        risk of morbidity and mortality in all four studies of
        sufficient size and duration where this could be evaluated. 
        Such an effect is of unquestioned clinical importance and
        such consistency cannot be attributed to chance alone.  The
        effect on the combined endpoint is the result of a
        concordant effect on the components of morbidity alone and
        mortality alone.
                 For these reasons, we believe that the effect
        of carvedilol on morbidity and mortality forms the
        principal basis for the approval of the drug for heart
        failure.  However, the benefits of carvedilol extend beyond
        morbidity and mortality, as I will now present data on the
        drug's favorable effects on symptoms and clinical status.
                 A discussion of the effects of carvedilol on
        symptoms and clinical status is inherently more difficult
        than the assessment of morbidity and mortality.  This is
        because measures of symptoms and clinical status are not
        well standardized, are subject to considerable observer
        bias, and are accompanied by a significant placebo effect. 
                 There is in fact considerable uncertainty as to
        how to measure the effect of a new drug on symptoms and
        clinical status.  No single measure has been developed that
        can accurately reflect the utility of a new agent.  Present
        measures assess three distinct but complementary aspects of
        heart failure, that is, the severity of symptoms, the
        impact of heart failure on the ability to exercise, known
        as functional capacity, or the impact of heart failure on
        general well-being and quality of life.
                 Each of these three aspects of the disease can
        be assessed either qualitatively or quantitatively.  The
        qualitative measures resemble the usual interaction between
        a physician and a patient in the clinical setting whereas
        the quantitative measures are primarily used in clinical
        trials.  Most of these measures of efficacy were utilized
        in the carvedilol development program.
                 With this in mind, I want to review the effects
        of carvedilol on the placebo-controlled trials carried out
        with the drug on symptoms and clinical status.  First I
        will focus on the three single-center studies.  
                 These studies were primarily designed as
        hemodynamic studies.  Each achieved its primary,
        prespecified endpoint, which was a measure of cardiac
        performance.  However, each trial also specified measures
        of symptoms and clinical status as secondary endpoints. 
                 The shorthand used on this slide and subsequent
        ones expresses the results in a placebo-subtracted change
        at study endpoint.  Positive changes favor carvedilol,
        negative changes favor placebo.  Results that are nominally
        significant at the p equal 0.05 level are highlighted in
        yellow.
                 Despite their small size and relatively brief
        duration, carvedilol had a significant effect on heart
        failure symptoms in both trials in which it was measured. 
        It also had a significant effect in two out of the three
        trials that measured New York Heart Association class.
                 In contrast, carvedilol had inconsistent
        effects on exercise tolerance.  The drug had no effect on
        maximal exercise capacity in any of the three studies, and
        it had equivocal effects on submaximal exercise capacity. 
        Studies 033 and BMI-01 assessed submaximal exercise
        capacity by observing the duration of exercise at 80
        percent peak effort, and carvedilol had a favorable effect
        in BMI-01, but did not have it in 033.
                 Only one study evaluated the effect of
        carvedilol on the 6-minute walk of the single center
        studies, and in this study the effect was significant.  The
        inconsistency of the effects of carvedilol on exercise
        tolerance was attributed to the known ability of beta-blockers to attenuate exercise performance.
                 Next I want to turn our attention to the
        effects of carvedilol on symptoms and clinical status in
        the multi-center trials carried out with the drug.  As you
        will recall, there were five multi-center trials but I want
        to focus your attention on four of the trials.  Because
        study 239 was terminated early and had only a brief
        duration of treatment, I will not discuss the specific
        results of this study, although those were presented in the
        briefing document.  Instead, I will focus on the other four
        studies.
                 First, study 240.  As you will recall, the
        primary endpoint for this study was morbidity and
        mortality.  However, this protocol also specified a variety
        of clinical measures as secondary endpoints.  
                 This slide shows the effect of carvedilol on
        symptoms and clinical status in this study.  As can be
        seen, carvedilol exerted a favorable effect on each of
        these measures, and this effect was statistically
        significant for New York Heart Association class, CHF
        symptom score, physician and patient global assessment.
                 For all qualitative measures of efficacy, more
        patients felt better and fewer patients felt worse with
        carvedilol than with placebo.  
                 Thus, the results of study 240 are consistent
        with the results of the single-center trials. 
        Specifically, carvedilol improved the symptoms and
        functional capacity of patients with heart failure, but had
        no effect on maximal exercise capacity.
                 Next, let us proceed to study 221.  In this
        study exercise tolerance, both near-maximal and submaximal,
        were specified as the primary endpoints, and the variety of
        clinical measures were specified as secondary endpoints. 
        By design, these clinical measures included the same
        measures of clinical efficacy assessed in the study I just
        showed, 240.  
                 Carvedilol had no effect on maximal exercise
        tolerance as measured by the 9-minute treadmill distance. 
        By the protocol-specified analysis, the drug had only a
        small effect on the 6-minute walk distance, which was not
        statistically significant.  However, this analysis excluded
        26 patients who did not have on therapy assessments, and
        imputed values for 23 others who did not complete the
        study.
                 Alternate approaches to this analysis that
        attempted to include a greater number of patients with less
        imputation of data are shown here for your interest.
                 This slide shows the effect of carvedilol on
        the prespecified secondary endpoints of symptoms and
        clinical status in study 221.  As can be seen, carvedilol
        exerted a favorable effect on all measures, and this effect
        was statistically significant for New York Heart
        Association class, physician global assessment, and patient
        global assessment.
                 As in the case of study 240, for the
        qualitative measures of efficacy, more patients felt
        better, fewer patients felt worse with carvedilol than with
        placebo.  
                 And adding these results onto the previous
        results I have shown, we can see that they are consistent
        with the single-center results, as well as with study 240. 
        Specifically, carvedilol improved the functional capacity
        of patients with heart failure but had no effect on maximal
        exercise capacity, and only small effects on submaximal
        exercise capacity.
                 Next, I will discuss the results of study 220. 
        Recall that this was identical in design to study 221,
        except for the number of treatment arms.  In this study
        there were three treatment arms for active drug,
        representing three separate doses.  The primary and
        secondary endpoints here, identical to study 221, were
        exercise tolerance, but this study was designed to evaluate
        the significance of the observed dose response
        relationships that compared carvedilol with placebo.
                 Because the effects of carvedilol on symptoms
        and clinical status were not related to dose, none of the
        primary analyses of study 220 were statistically
        significant.  
                 However, when all of the doses were combined
        and compared with placebo, there was a parallelism between
        the effects of carvedilol shown in study 221, which I
        previously displayed, and the effects in study 220 for a
        number of the endpoints.  This is not too surprising since,
        again, these two studies recruited the same types of
        patients and had a similar design.  
                 Finally, I would like to present the results of
        study 223.  You will recall that this study had two
        principal objectives, a short-term one, based on clinical
        and physiologic measures, and a long-term one based on
        morbidity and mortality.  Measures of symptoms and clinical
        status were not described in the protocol but were
        collected in the case record form.
                 Although there was a mild tendency for
        worsening on carvedilol after 6 months, this was no longer
        present after 12 months of treatment, and the results for
        12 months are shown here.  For all three measures, there
        was little difference between carvedilol and placebo.  In
        part, this can be attributed to the large number of
        minimally symptomatic patients in this study who
        mathematically could not improve.
                 Lastly, I want to present the effects of
        carvedilol on a measure of clinical status that was used in
        all of the U.S. multi-center trials:  the global assessment
        of well-being.  This measure requires both the patient and
        the physician to ascertain how in general terms the patient
        is doing compared with the patient status at the start of
        the study, so it's a relative measure.  This simple measure
        closely resembles the discussion that normally takes place
        between patients and physicians in an office setting.  
                 Here I summarize the effect of carvedilol on
        the global assessment using the protocol-specified
        approach.  An up arrow indicates the percentage of patients
        who improved in a given treatment arm, and a down arrow
        indicates the percentage who worsened.
                 In each of the three largest U.S. multi-center
        trials, regardless of whether the assessment was by the
        patient or by the physician, more patients improved and
        fewer patients worsened on carvedilol compared to placebo. 
        The effect was statistically significant or nearly so in
        all six assessments.
                 This slide summarizes the effects of carvedilol
        on symptoms and clinical status.  Carvedilol produced a
        consistent improvement in CHF symptoms, a consistent
        improvement in NYHA class, and a consistent effect on
        overall well-being, but only small effects on exercise
        tolerance and quality of life.  The effects of carvedilol
        on CHF symptoms, NYHA class, and overall well-being were
        nominally significant in a number of trials.  
                 In addition, in each of these four trials
        carvedilol improved at least three different measures of
        clinical efficacy.  Two of these trials were single-center
        studies, and two of the trials were multi-center studies.
                 We understand that we should be cautious in
        interpreting an effect on a secondary endpoint that did not
        reach significance on the primary endpoint, but we should
        note that in all four of these studies the effect of
        carvedilol on the primary endpoint was statistically
        significant, or nearly so.
                 In studies 035 and BMI-01, carvedilol improved
        the primary endpoint of cardiac function.  In study 240,
        carvedilol achieved the primary endpoint of morbidity and
        mortality, and in study 221, carvedilol improved the
        primary endpoint of 6-minute walk distance.  This pattern
        of consistency within and across studies is unlikely to
        have occurred by chance alone, and supports the favorable
        effect of carvedilol on morbidity and mortality.
                 Upon the request of the FDA, we will not be
        presenting detailed information about the safety of
        carvedilol because the FDA has not raised any safety
        concerns about the use of carvedilol in heart failure in
        the clinical trials.  Full information about safety is
        contained in the briefing document provided to the
        committee.  We do wish to emphasize the following points,
        though.  
                 First, that carvedilol was safe and well
        tolerated in the clinical trials when used with caution,
        when up-titration was guided by specific algorithms and
        when investigators were fully educated about the risks.  In
        the absence of these measures, the relationship of benefit
        to risk may be considerably altered.
                 Second, side effects are frequent during
        initiation of therapy, but these can be managed in most
        cases by careful titration of carvedilol and by changes in
        the doses of concomitant medications.                  
                 Third, unlike many other drugs evaluated for
        heart failure, carvedilol exerts no adverse effect on
        survival.
                 In conclusion, we have demonstrated that
        carvedilol produces improvement in each aspect of the
        hierarchy of the evaluation of heart failure.  
                 First, carvedilol has substantial effects on
        cardiac function in patients with heart failure.  Ejection
        fraction was improved in all eight placebo-controlled
        trials carried out with the drug and is accompanied by a
        favorable change in cardiac dimensions.
                 Second, carvedilol produced consistent effects
        within and across studies to improve the symptoms and
        clinical status of patients with heart failure.  This was
        shown best on the qualitative measures of patient
        assessment such as symptoms, New York Heart Association
        class, and global assessment.  These situations most nearly
        reproduce the usual clinical interaction between a
        physician and a patient.  
                 And third, carvedilol produced substantial
        effects on the unquestionably important endpoints of
        morbidity and mortality, as shown in this summary slide. 
        These benefits are observed consistently across the
        controlled trials carried out with the drug, regardless of
        the definition used, and additional analyses requested by
        the FDA confirm the robustness of this effect.
                 Therefore, based on all the data presented
        today and the documents submitted to the committee, the
        carvedilol SNDA meets the usual standard employed to
        conclude that drugs are effective in the treatment of heart
        failure.  
                 Thank you.
                 DR. DiMARCO:  The schedule calls for a break
        now, but I think in view of the time, the fact that we
        started at 2:15, we'll continue until about 4 o'clock
        before we take a break.
                 Dr. Lipicky, do you or any members of the
        division wish to say anything at this point?
                 DR. LIPICKY:  No.
                 DR. MOYE:  Can I ask a question of the FDA?  Is
        it true that the issue of medication status has been
        resolved to your satisfaction in study 240?
                 DR. LIPICKY:  That's a very complicated
        question.  I guess the short answer is yes.  
                 The long answer is that, depending on what you
        do, you see there are slightly different p values
        associated with the analysis.  Regardless of want you do
        and what you assume, it's always got better than a nominal
        p of .05.
                 DR. MOYE:  So, regardless of what you do, the p
        value winds up being less than .05.
                 DR. SHUSTERMAN:  But Dr. Moye, the issue that
        arose last time, whether the FDA had executable files to
        run algorithms has been solved.
                 DR. LIPICKY:  Okay, fine.  Let me say, the
        problem was that in the original data that we obtained --
        we had all of the original data that was to run analyses
        ourselves.  The data in those files regarding the
        medications was in our judgment not sufficiently obvious to
        be able to decide what the basis for decisionmaking was.
                 Those files were sent.  We don't think it's a
        big issue.  Did I say something wrong?  And so okay, I was
        just checking with the reviewers, and they say we don't
        think that's a big problem.
                 DR. DiMARCO:  Dr. Temple?
                 DR. TEMPLE:  The reason it's not a big problem
        is that we did an extremely conservative analysis based on
        the small fraction of patients whose medications were
        thought to be adequate, the result of which was to greatly
        reduce the data set, but it was still significant at the
        usual level, even doing that, which is very adverse when
        you do an analysis for only about a third of the patients.
                 DR. DiMARCO:  Dr. D'Agostino?
                 DR. D'AGOSTINO:  Can I ask a couple of
        questions?  I wasn't here for the previous discussion so
        you have to excuse me if I ask the same questions as were
        already asked and clarified.  
                 I have a couple of problems with the idea of
        having as an endpoint death due to CHF as opposed to all-cause mortality.  You've done both.  Also the
        hospitalization.  But in the analyses or in the studies
        where you actually did do the hospitalization due to CHF
        and the death due to CHF, could you just say some words
        about how you decided somebody dies of CHF and
        hospitalizations?
                 DR. SHUSTERMAN:  The technical answer is that
        the investigators coded the deaths when they occurred and
        coded the hospitalizations.  They were then reviewed
        internally in a blinded fashion to ensure that deaths that
        reasonably could be considered also to be CHF were not
        excluded.  But it turns out the majority of the deaths, 70,
        75 percent, would be considered related to heart failure,
        either a sudden death, which is why we included that
        definition, or worsening of the signs and symptoms
        ultimately leading to death.
                 DR. D'AGOSTINO:  One of your analyses that has
        a nice p value with it represents four deaths in one group
        and zero in another group.  I sit on the Framingham
        committees where we try to figure out what people are dying
        of.  My sense of our imprecision would put a few of the
        zeroes, deaths suddenly.  That group would probably have
        quite a number that might be related to CHF.
                 I like the all-cause mortality and I like the
        hospitalization for the sort of all-cause or the CVD
        hospitalization.  Just what I am trying to clarify is I
        don't think we should keep jumping back and forth between
        the two because I think there are problems with the CHF
        hospitalization and mortality.
                 DR. DiMARCO:  I think Dr. Califf has a comment
        here.
                 DR. CALIFF:  I just want to stay on this line,
        and just for understanding because I really agree with
        Ralph and I would hope that maybe we could quickly dispose
        of cause-specific endpoints in the discussion.  
                 But just to be sure, you said they were
        internally reviewed also.  By whom, and was the internal
        review bonded?  And are the data you are presenting the
        internal review or the investigators' call on the cause-specific endpoints, both death and hospitalization?
                 DR. SHUSTERMAN:  The internal review was done
        by the medical monitors for the trials.  It was done before
        the blind was broken.  And what was the last part of your
        question?
                 DR. CALIFF:  The data you presented, is it the
        investigators' call or is it the internally reviewed call?
                 DR. SHUSTERMAN:  The more conservative call was
        used, so if the investigators excluded a death and ours
        included it, we would include the death, or the
        hospitalization.
                 DR. DiMARCO:  Dr. Temple, you had a comment?
                 DR. TEMPLE:  There is a slight problem in your
        preference for all-cause mortality.  It wasn't the
        identified primary endpoint, so you get into a bit of a
        box.  We don't disagree with you at all, but in study 240,
        the identified endpoint was --
                 DR. D'AGOSTINO:  No.  I understand that.  240
        is 240, and we make whatever we can out of that, but we're
        going to move to looking at mortality across these studies.
                 DR. TEMPLE:  That actually helps a lot.
                 DR. DiMARCO:  Dr. Borer.
                 DR. BORER:  When the multi-center study was
        stopped all the patients on placebo were offered
        carvedilol.
                 DR. SHUSTERMAN:  That is correct.
                 DR. BORER:  I don't know how many of them took
        it, and I don't know whether you followed these patients,
        but that's going to be my question.  And I understand fully
        all the problems associated with looking at data you didn't
        expect to look at and all that.
                 Just my own information, if you have the data,
        it would be of interest to me to know whether a substantial
        majority of the patients who were on placebo took the
        carvedilol and if you followed them.  And if you did follow
        them, was there an upward break in the survival curve in
        that previously placebo-treated group.  So that it would
        approach the carvedilol curve.  Do we know that?
                 DR. SHUSTERMAN:  I can tell you that greater
        than 90 percent of the patients in both arms at the time
        the trials were discontinued, continued on open label
        carvedilol.  We have done the analysis that you have
        suggested.  That is, look at the mortality in patients
        previously on placebo, switched over to carvedilol. 
                 As you can imagine, because it's not a
        concurrent control, it is, I think, a sloppy analysis, but
        the curve for those patients for mortality tracked the
        group that started on carvedilol.  That we have on a slide
        and there it is.
                 The lowest line is placebo during the double-blind trials.  This is carvedilol during the double-blind
        trials, and this line is patients previously on placebo
        switched over to carvedilol.  The numbers drop off after
        about a year or so here when this analysis was done, so I
        wouldn't pay too much attention to the tails, but for the
        first part of the curve virtually overlapping the original
        carvedilol.
                 DR. COLUCCI:  If I could just add, this data,
        this analysis was exactly as shown here, shown at the
        American Heart Association meeting in November.  The other
        interesting line there are the patients on drug who have
        now been followed for a median time of over 2 years.
                 DR. DiMARCO:  Could you please identify
        yourself, sir?
                 DR. COLUCCI:  Wilson Colucci.  I was the PI of
        study 240.  
                 So, I just wanted to amplify a little bit on
        this data.  This was an analysis undertaken by the
        investigators and presented as an abstract at the American
        Heart meeting last November.
                 Then to amplify further, the treatment group,
        who have now been continued for a median treatment of over
        2 years, have continued on a virtually identical trajectory
        to that shown there.  
                 DR. KONSTAM:  And, Bill, which trials are
        represented in these?  Are these all four U.S. trials?
                 DR. COLUCCI:  These are all of the patients in
        the U.S. carvedilol trials.
                 DR. SHUSTERMAN:  That is correct.  This is a
        combined.
                 DR. DiMARCO:  Dr. Califf?
                 DR. CALIFF:  I have a couple of questions. 
        Maybe I should go to the last one first because I don't
        know if you have the data handy.  
                 What would help me the most would actually be
        to have the actual data for death and all-cause
        hospitalization for all the studies that have been done. 
        It seems like it's been hard for me to follow.  There's so
        much jumping around.  But if we just had all-cause
        mortality and all-cause hospitalization with the number of
        patients, the number of events, and the odds ratios for
        each study and then combined, I think that would give us a
        very nice way of looking at the data in an unambiguous way
        that would get us out of this flipping back and forth.
                 I don't know if you have the data handy.  It
        seemed like one of the slides you showed almost had all of
        it but not quite.
                 DR. SHUSTERMAN:  The last slide showed it
        obviously graphically in terms of the relative risk and the
        confidence intervals as lined, but you want the actual
        numbers.
                 DR. CALIFF:  It didn't have all the studies. 
        It was missing at least one.  
                 DR. SHUSTERMAN:  It was only missing 239.  That
        was the small study that was terminated early and had about
        3 months of follow-up.  But if we could put the last slide
        on.
                 DR. CALIFF:  If there's a way to get at the
        actual numbers, it would help me, and you'll understand why
        when I ask the next couple of questions.  The odds ratio
        plots look nice but the numbers are not there.
                 Let me go ahead with the other questions while
        you're looking for the slide.  
                 This is a simple technical question I'm sure
        you've dealt with already in terms of the left ventricular
        function endpoints.  How many missing values did you have,
        and what did you do with the missing values in the analysis
        in terms of people who died or people who had inadequate
        studies, or just didn't come back?
                 DR. SHUSTERMAN:  You're talking about for
        ejection fraction?
                 DR. CALIFF:  Yes.
                 DR. SHUSTERMAN:  For ejection fraction, that
        represents all patients with a baseline and an on-therapy
        value.  So, we did not impute data for patients who were
        missing and we didn't carry forward baseline values for
        those who didn't have an on-therapy value.
                 DR. CALIFF:  The concern is obviously the
        people who were sicker were more likely to die and not come
        back, and so the natural outcome of a study where you had
        deaths would be that the ejection fractions would go up,
        since the patients who were better off were more likely to
        be alive. 
                 Of course, you have a comparison with a control
        group, a placebo group.  I'm just wondering if you did any
        worst case kind of analyses to account for that.
                 DR. SHUSTERMAN:  Well, we did not do a worst
        case analysis on ejection fraction because we provide that
        data to help explain the hemodynamic effect of the drug,
        but as has been shown earlier, that's not the basis that
        we're seeking approval for.
                 DR. CALIFF:  But the same would hold for
        symptomatic status.
                 DR. SHUSTERMAN:  Well, for symptomatic status
        we actually have done those analyses and when you do that
        kind of effect, that is put in worst case for a patient who
        drops out, then actually the results look better than I
        have shown here.
                 DR. FISHER:  Rob, your argument is correct. 
        People who die are more likely to have low ejection
        fractions, but there are more deaths in the placebo arm,
        and it was compared to placebo, which would tend to bias
        against the active therapy --
                 DR. DiMARCO:  Could you please identify
        yourself, sir?
                 DR. FISHER:  -- if you have a superior
        survival. 
                 DR. CALIFF:  Lloyd Fisher.  I'll identify him.
                 (Laughter.)
                 DR. CALIFF:  But that's an indirect argument.
        I'm really just asking whether you directly address the
        problem in the analyses.  It's also true that people who
        are sicker, feeling worse, are less likely to come back to
        get their non-invasive study.  
                 I'm just asking if there were any direct
        analyses done.  It sounds like there weren't.
                 The last question is, I'm really hung up on the
        run-in phase, and this was probably reviewed last time and
        I wasn't here.  
                 But it seems to me that our charge is to try to
        answer the question, would we recommend this as a therapy
        for a physician and a patient with heart failure, who
        doesn't have the opportunity to go through a run-in phase
        before things start to count.
                 I don't really know how to deal with that.  I
        don't know how to put a study in which all the patients
        that had bad things happen are eliminated before you start
        the treatment.  I'm sure that you must have done some
        indirect analyses to try to sort of take that into account,
        but it's a bothersome thing that I hope the committee and
        the clinicians and statisticians will help me out with.
                 And the reason it's important to me and the
        reason I keep asking for numbers is that the differences --
        all of the p values are small.  The numbers of events are
        also relatively small.  And if you did a worst case
        analysis, for example, and counted all the deaths and all
        the drop-outs as attributable to the treated group, I
        wonder what the results would look like.
                 DR. SHUSTERMAN:  Before we show that slide,
        could we hold up on that slide because I want to address
        that question.  I think you raised some really important
        issues there.  
                 The first is, the use of a run-in design is not
        at all unusual and in fact, it has been preferred at times
        by the FDA because it actually enhances the power of the
        trial.
                 Of course, that leaves you with the dilemma,
        what to do with the events during that time and you have
        stated that.  The problem there is, of course, there is no
        control to compare against.  You don't know whether to
        attribute an event to the drug, to the patient's underlying
        disease, or to the phase of the moon.
                 But what we have done and what we believe is
        that the most appropriate analysis, where there is a
        control, is from the point of randomization.  
                 Nonetheless, we've done several analyses and
        Dr. Fisher can speak to the one on mortality, where we have
        included the run-in events, and they do not affect the
        overall effect of carvedilol.  We've done that on 240, 223,
        and the overall mortality.  I think maybe Dr. Fisher would
        like to speak about mortality.
                 DR. FISHER:  I think it's a very important
        issue and I agree it's debatable whether there should be
        run-in periods of mortality trials because as nice as
        enrichment trials are in certain situations, here you worry
        you help some people but other people you hurt.  The net
        effect is zero, but you kill off the high risk people early
        so they're not in the trial when you randomize.
                 I thought this was going to come up last time
        and I brought a lot of data.  I don't have my data with me
        but I can tell you the results of my analysis and then the
        agency statisticians can check it when they get done.
                 I did a lot of analyses, and what I did was
        compared both the overall mortality rate on carvedilol
        during the run-in period with the carvedilol patients
        during the trial and they were the same.  Of course, you
        don't have incredible statistical power, but there was no
        directional trend or anything.  It looked the same.
                 And looking at the very short early survival
        curve, because that's all you have in the run-in period, it
        looked the same.  
                 So, there's no indication whatsoever that a
        high-risk group was eliminated differentially because to me
        that was a very important concern.  And I think it
        potentially could be very important in a setting such as
        this, and I was surprised it didn't receive more attention
        last time.
                 DR. MOYE:  Lloyd, just to follow up.  What
        would happen if you assumed very conservatively that all of
        the patients who died in their run-in period would have
        wound up in the active group and all the survivors wound up
        in the placebo group?
                 DR. FISHER:  Well, it would have shifted things
        in the opposite direction than if I had assumed they all
        would have ended up in the placebo group and died.
                 DR. MOYE:  But do you think that the p value
        would have changed substantially from what was reported for
        total mortality for the U.S. studies?
                 DR. FISHER:  To me, Lem, to be honest, this is
        an irrational analysis. 
                 DR. MOYE:  It's a very conservative analysis. 
        Whether it's irrational or not I don't know.
                 DR. FISHER:  We can all agree to that. 
                 I haven't done that, so I don't directly know
        the answer to that.  Maybe somebody else has.  But all I
        can tell you is I compared, as best I could, the rate and
        there was no indication of an elevated mortality rate on
        carvedilol during the run-in period.
                 DR. CALIFF:  I'll buy that.  I'm not
        challenging that you did that.  You would agree -- and I
        sense a little uncertainty on your part -- that it's a
        little hard to say, I'm going to give you this treatment
        and if you make it through the first 2 weeks, then we've
        proven that things will be better.  That's not ideal.
                 But it looks like there are about 15 deaths in
        the run-in phase.  The document has a nice summary of the
        run-in phase of each study.  It looks like about 15 deaths,
        and you could pretty well --
                 DR. SHUSTERMAN:  Seven deaths in the U.S.
        placebo controlled multi-center trials.  Seven deaths.
                 DR. CALIFF:  There are 4 in study 035 in the
        run-in phase, and then there are 2 deaths in the New
        Zealand study.
                 DR. SHUSTERMAN:  That's right.  Two deaths,
        plus seven.  We presented the U.S. multi-center phase and
        the Australian-New Zealand.
                 DR. CALIFF:  I actually got 9.  Well, anyhow,
        between 13 and 15 deaths.
                 DR. PACKER:  This is Milton Packer.  
                 Your question I think relates to whether there
        were a number of run-in events and were they of significant
        number, given the numerators, the total number of events in
        the trial because it's hard to know how to make these
        adjustments for run-in events, but if the numbers are small
        then I guess everyone would be reassured.
                 I'm trying to get the exact numbers, but I can
        give you something that I think is within about 10 events,
        and we'll get the exact numbers for you in just a few
        minutes.  
                 But over all the placebo-controlled trials,
        there were about 400 deaths and hospitalizations for any
        cause.  In the placebo group, it was 200 over 604, and the
        carvedilol group about 190 over 903.  That's a 32 percent
        event rate in the placebo group, a 21 percent rate in the
        carvedilol group.  You have already seen the p value is
        .00001.  But we are talking about 400 events.
                 DR. CALIFF:  But if we look at those who
        dropped out in the run-in phase -- and about half of those
        appear to be due to either death or heart failure -- that's
        going to be about 120 to 140 additional events, divided by
        half, maybe 70. 
                 I'm not saying I know what to do with this. 
        It's just a point of discomfort.  I've said enough and I'll
        stop it now.  But I hope that people on the panel will help
        me understand how to deal with this.
                 DR. DiMARCO:  Ralph?
                 DR. D'AGOSTINO:  I'd like to ask another
        question about study 223.  I'm not clear on this long-term
        follow-up piece.  Were the individuals still under a
        double-blind regimen, or was it an open-label component? 
        It's not clear to me.
                 DR. SHUSTERMAN:  That's a good question.  It
        was double-blind treatment for the entire 18 to 24 months
        of the trial.  
                 DR. D'AGOSTINO:  So, all of the analysis --
                 DR. SHUSTERMAN:  No open-label at all.
                 DR. D'AGOSTINO:  Can I ask one more question? 
        It's unfair, but let me ask it.  
                 Do primary events mean nothing in the company? 
        What is the company policy when they run a study and the
        primary events do not turn out to be significant?  Is it
        then assumed that you can ignore them?
                 This is a philosophical question, but I'm
        trying to get a sense of how I'm to respond to these post
        hoc and retrospective analyses in the presence of a non-significant primary.  
                 Could you tell me what you would do?  Would you
        multiply something, a multiplicative factor for the
        analyses you've done?  Or would you just ignore it?
                 DR. SHUSTERMAN:  I'm going to ask Dr. Jim
        Tiede, who's head of biometrics at SmithKline to address
        that.
                 DR. TIEDE:  Ralph, I'm not quite sure which
        studies you're referring to, but if it's studies 220 and
        221, we looked at those as more confirmatory information. 
        We had the prespecified endpoints for 240 and 223, but then
        wanted to see if that would hold up when we looked at other
        trials.  So, it wasn't that we were ignoring the primary
        endpoint.  We recognized that we didn't achieve it.  We
        were looking just to see, did those studies provide a
        result that was contradictory to the two primary studies.
                 DR. DiMARCO:  Dr. Lipicky, do you have a
        comment?
                 DR. LIPICKY:  Milton, those numbers of 400,
        that was for all kinds of events?
                 DR. PACKER:  No cause-specific.  This is the
        most conservative, no-bias interpretation.
                 DR. LIPICKY:  I just looked at studies 240 and
        239 and for deaths, all told there were 10.  A big jump to
        400.
                 DR. PACKER:  There were a lot of
        hospitalizations.
                 DR. LIPICKY:  I see, so that's in
        hospitalizations --
                 DR. PACKER:  And hospitalizations, which is the
        -- and it's all-cause mortality and all hospitalizations.
                 DR. LIPICKY:  Well, that was 10 all-cause
        deaths I was talking about.
                 DR. PACKER:  Yes.  The total number of deaths I
        believe in the U.S. program, all-cause, is 53 and in
        Australia-New Zealand it's about 55 I believe.  It's a
        little over 100 events so that 25 percent of the all-cause
        deaths and all-cause mortality is mortality, and 75 is all-cause hospitalization.
                 DR. KONSTAM:  So, could we complete the story
        about if you want to call it a numerator of the events in
        the run-in phase again in like terms.  So, the total number
        of deaths in the run-in phase were 9?
                 DR. PACKER:  Nine.  Seven in the U.S. study, I
        believe 2 in Australia-New Zealand.
                 DR. KONSTAM:  Compared to about 50 --
                 DR. PACKER:  About 100 combined, 110 combined.
                 DR. KONSTAM:  110 combined what?
                 DR. PACKER:  U.S. and Australia-New Zealand. 
        Deaths.  
                 Just to go through it again, total number of
        run-in deaths in all multi-center trials is 9.  Total
        number of deaths in the multi-center trials is
        approximately 110.  Total number of deaths and
        hospitalizations -- and we're working to get the precise
        numbers -- is between 25 and 30.  Total number of deaths
        and hospitalizations all across the same corresponding
        analysis is in excess of 400.
                 DR. KONSTAM:  I was under the impression that
        you had done an analysis.  Let's just stick to mortality
        for a second with that worst case scenario of applying all
        the deaths to the carvedilol group.  Was that analysis not
        done?
                 DR. PACKER:  Yes, an analysis was done, and
        showed that even if you took all the deaths and attributed
        it to carvedilol, which would be the most conservative
        analysis, the effect was still statistically significant. 
        The same analysis has been done for 240 and for 223.
                 DR. KONSTAM:  Milton, what did it do to the
        nominal p value?
                 DR. PACKER:  .01, if I remember correctly. 
        You're taking all the events, attributing it to one
        therapy.
                 DR. KONSTAM:  All the deaths.
                 DR. PACKER:  All the deaths, attributing it to
        one therapy.  .01.
                 DR. SHUSTERMAN:  And we can show that.  If we
        can bring up prime 14, we have that.
                 This is the analysis if you include all deaths
        during run-in, attribute them to carvedilol.  The relative
        risk is shown there.  I can't read it quite from here but
        maybe you can.  And the p value, as Milton said, was .0108.
                 DR. CALIFF:  Again, this only includes four
        studies, it looks like. 
                 DR. SHUSTERMAN:  This is for the U.S. multi-center program.  We did it for the U.S. multi-center
        program.
                 DR. DiMARCO:  So, it doesn't include the 2
        deaths in New Zealand and the 4 deaths in the 035?
                 DR. PACKER:  035 had 5 deaths and, again, that
        was in favor of carvedilol.  Please remember, 035 had a 2
        to 1 randomization.
                 DR. CALIFF:  During the run-in phase, Milton,
        for 035, I think it said there were 4 deaths in the run-in
        phase.
                 DR. PACKER:  Gee, that's my study.  I should
        know, huh?
                 DR. SHUSTERMAN:  I can tell you, across all of
        the trials we have not done this analysis.  We have done
        this for the multi-center trials, and that's what you see
        here.  This counts the 7 run-in deaths against carvedilol.
                 DR. DiMARCO:  Dr. Moye?
                 DR. MOYE:  My understanding of protocol 223 is
        that the primary endpoint was an exercise tolerance
        endpoint.  Do you disagree with that?
                 DR. SHUSTERMAN:  Protocol 223 had two distinct
        phases.  I think that's pretty clear from the way the
        investigators set up the trial.  
                 Exercise left ventricular ejection fraction and
        left ventricular size were measured at 6 and 12 months, but
        morbidity and mortality was measured throughout the entire
        18 months of the trial.  In fact, none of those three
        measures that I mentioned were ever done again after the
        12-month point of the trial.
                 DR. MOYE:  Well, I'm confused.  Let me read you
        a statement from the protocol.  "The proposed study of 450
        patients is not expected" -- I say again, not expected --
        "to provide any reliable evidence about the effects of
        carvedilol on survival.  Several thousand patients followed
        for several years would be necessary for the reliable
        detection of plausibly moderate treatment benefits.  Such a
        study would be proposed if the results in this present
        trial indicate that carvedilol was well tolerated by a
        large proportion of the study population."
                 DR. SHUSTERMAN:  That is precisely correct. 
        This was not a mortality trial, and that's a very important
        point, and obviously was extremely underpowered to be a
        mortality trial.  We're talking about the combined endpoint
        of morbidity and mortality, and for that the trial
        following patients for 18 to 24 months, some 415 patients,
        was an appropriate vehicle for that endpoint.  That was the
        purpose for the follow-up of that length and duration,
        especially after no other measurements of status were
        performed after 12 months.  
                 So, this was not a mortality trial.  The
        protocol is totally correct.  We are not bringing it here
        as a mortality trial.  But the protocol specifically said,
        and I gave you the quote, that mortality and major
        morbidity were to be looked at over the entire 18 months.
                 DR. MOYE:  Well, again, I must say, I'm
        confused by other statements in the protocol because they
        seem to, from my point of view, contradict this.  Another
        statement says, "The major objectives of the study are to
        determine the effects of this treatment on exercise
        capacity, left ventricular function, and left ventricular
        size after 6 and 12 months of treatment."
                 DR. SHUSTERMAN:  That indeed was the major
        objective for the short-term phase of the trial, and they
        were measured at that time point.
                 DR. MOYE:  I can find no statement in here that
        says that a portion of the primary endpoint is for combined
        morbidity and mortality, with a statement about the
        definition of morbidity.  I mean, to me it all seems
        extremely vague and very general, which is very curious for
        the statement for a primary objective.  Do you disagree
        with that?
                 DR. SHUSTERMAN:  The protocol as written by the
        investigators is vaguer than I think you or I would have
        ideally liked to see.  This was written some six years ago
        by them, and the protocol was initiated by them also.  But
        it was clear that a long-term phase was a major aspect of
        this trial.  Just because the patients were followed for so
        long with the express purpose.  And that purpose has been
        stated by the investigators, not only the quote that I have
        in the protocol, but in additional communications.
                 If I could have prime slide 2.  Their initial
        short-term phase results were published in Circulation, and
        this manuscript was submitted in January 1995.  
                 Now, following completion of the short-term
        phase of the trial, and the observation that carvedilol had
        no adverse effect on exercise capacity or left ventricular
        function or size, the decision was made to continue
        treatment and follow-up of study patients with the main
        objective of determining the effects, if any, of treatment
        with carvedilol on hospital admission and mortality.
                 So, this is in the protocol.  This was a
        specific, active decision that was made for the long-term
        purpose of the trial.  
                 If I could have the next slide, please.
                 DR. MOYE:  Just a second, please.  If I read
        this right, the decision was made to continue -- and please
        tell me if I'm wrong.  The decision was made after the
        trial started to continue to the long-term follow-up.  Is
        that right?
                 DR. SHUSTERMAN:  The decision was made to not
        stop the trial, to allow it to continue for 18 to 24
        months.  It was pre-written into the protocol that they
        would look, and if there was an adverse effect on the 6 and
        12 months, that the protocol could be stopped.  So, the
        protocol from the start was 18 months with the ability to
        stop it if there was something bad happening.
                 DR. MOYE:  But there was no stated endpoint at
        18 months, no well-defined endpoint?
                 DR. SHUSTERMAN:  Yes, if we could have the next
        slide.  This is the correspondence with the principal
        investigator in the trial, and the definition of the
        endpoint mortality and major morbidity is shown here.  The
        definition that we adopted for this outcome was death from
        any cause, or hospital admission for any cause, during the
        period between randomization and the end of follow-up.
                 And secondly, when was this decision made?  The
        decision to use this global index of mortality and major
        morbidity was made prior to unblinding the data on these
        outcomes.
                 DR. MOYE:  It was made after the trial was
        started, but prior to unblinding.
                 DR. SHUSTERMAN:  After it started, before it
        was unblinded.  Based on what was said in the protocol
        about mortality and major morbidity.
                 DR. MOYE:  Okay.  Well, then would you have any
        response to the criticism that the investigators had a
        sense of how things were going and therefore tailored their
        definition for morbidity based on their sense for the
        direction of the data?
                 DR. SHUSTERMAN:  Well, I would say that if they
        used a cause-specific definition, Dr. Moye, but here they
        picked the broadest, least-biased, most assumption-free. 
        All deaths, all hospitalizations.  It didn't matter what
        they were admitted to the hospital for.  So, I think that
        has the least bias in terms of being influenced by anything
        they knew during the trial.
                 DR. PACKER:  And then this decision to go
        forward after the completion of short-term phase is
        specifically mentioned in the original protocol.
                 Lem, the decision to go forward with the long-term phase was specifically mentioned in the original
        protocol.  The original protocol said that data on
        mortality, major morbidity would be collected for 18
        months, extended by a protocol amendment to 24 months.
                 Then later on in the protocol it says that
        decision would hold unless at the completion of the short-term phase there was an adverse effect on the exercise
        tolerance or LV chamber-size dimensions, ejection fraction
        measured during the short-term phase.
                 Everything you've seen here was prespecified in
        the original protocol.
                 DR. MOYE:  Except for the definition of
        morbidity.  Right?
                 DR. PACKER:  I think that if you and I would
        recognize that the definition of mortality and major
        morbidity needs to defining in this protocol, because it is
        not clear from the protocol what it is, what we can be
        reassured by is, one, they used the broadest, least-biased
        definition possible.  And two, they defined it before they
        had any knowledge of any of the treatment effects before
        the blind was broken.
                 I think it's perfectly consistent with the way
        the clinical trials are run.  If there is anything vague in
        the protocol that needs defining, you define it up front,
        you define it in the least-biased way possible, and you
        define it before you break any codes.
                 DR. MOYE:  The message I get from you, then,
        not to belabor this, is that the decision for a follow-up
        study was made before the trial started, but the decision
        as to the composition of the morbidity endpoint was not. 
        But it was made before the results were unblinded.
                 DR. PACKER:  The fact that there was such an
        endpoint for the long-term phase was prespecified in the
        original protocol.  The precise definition of what
        morbidity/mortality would be was made before the blind, as
        you have said, after the original protocol, but I think
        that it was made quite fairly.  It's the broadest
        definition of morbidity and mortality one can think of.
                 DR. DiMARCO:  I'm glad you both agree. 
                 Dr. Borer?                                   
                 DR. BORER:  I don't want to belabor the run-in
        phase mortality issue.  You've been very forthcoming about
        the data and the analyses that you did to try to deal with
        this, but I would like to know more precisely what kind of
        analysis was done.  The primary outcome analyses were time-varying analyses, and these events occurred before time
        zero.
                 What did you do?  Add all the patients from the
        run-in phase who died as carvedilol patients and assume
        they died at time 0?  Or was some other kind of analysis
        performed?
                 DR. SHUSTERMAN:  It was a time-to-event
        analysis but instead of starting the clock, so to speak, at
        the point of randomization, it was started at the point of
        the very first dose of carvedilol during the open-label
        period for all of the patients.  Patients who died were
        attributed to carvedilol.  Patients who lived and went to
        placebo were attributed to placebo.  So, it was from the
        very first dose.
                 DR. BORER:  I see.  Thank you.
                 DR. KONSTAM:  And what's the statistical test?
                 DR. SHUSTERMAN:  Log-rank test.  That was a
        Kaplan-Meier curve.
                 DR. DiMARCO:  Dr. Califf?
                 DR. CALIFF:  Again, I know we are belaboring
        this, but that's been done for all of the trials with all
        of the patients.  Has it or has it not?
                 DR. SHUSTERMAN:  For deaths it has not been
        done for all of the double-blind trials.
                 DR. CALIFF:  What about death and all-cause
        hospitalization?
                 DR. SHUSTERMAN:  But it has been done for the
        U.S. multi-center program, which was the major component of
        all of the trials.
                 DR. DiMARCO:  This is 4:05.  We'll take a 10-minute break now and reconvene at 4:15.
                 (Recess.)
                 DR. DiMARCO:  I'd like to get started.  Before
        I poll the committee and ask if there are any additional
        questions, I'd like to ask the division if they have any
        questions for the sponsor.
                 DR. LIPICKY:  No.
                 DR. DiMARCO:  Would any of the reviewers like
        to say anything at this point?  The medical or statistical
        reviewers?
                 DR. D'AGOSTINO:  I want to make a comment.  Oh,
        you're talking about the FDA reviewers.
                 DR. DiMARCO:  The FDA reviewers.
                 DR. D'AGOSTINO:  I would think that it's
        important to hear one of the FDA people make a
        presentation.  They have quite a different spin on some of
        these data.  We could pick it up on our own, but I think
        it's important to hear them say something.
                 DR. RODEN:  While people are coming to the
        microphone, can I ask what kind of criteria people used to
        decide --
                 DR. DiMARCO:  Dan, why don't we do the FDA
        reviewers first and then we'll get to your question.
                 DR. STOCKBRIDGE:  I'm Norman Stockbridge, FDA.
                 I don't have anything new to offer on the basis
        of what we heard this morning.  I think you have our
        reviews and know what our biases are here.  If you have
        specific questions that you want to ask us, we can
        certainly respond to that.
                 DR. DiMARCO:  Rob?
                 DR. CALIFF:  Maybe you could just say a few
        words about your assessment of death and all-cause
        hospitalization, and your view about the run-in phase and
        analyses that you did on that.
                 DR. STOCKBRIDGE:  The issues about run-in
        phase, I think we were fairly satisfied that the point
        estimate one has of the mortality rate specifically during
        the run-in phase was not much different from what you saw
        during the trial.  So, it wasn't like there was a large
        effect, and a lot of people who were at risk of dying as a
        result of exposure to the drug got filtered out through
        that.  I think we were fairly satisfied with that.  
                 We were also satisfied, I think, that there was
        no large rebound effect associated with coming off of the
        drug and going into the placebo group.  The early mortality
        rate in the placebo group was not unusually high.  I don't
        believe we have done any analysis that tried to look at
        death plus hospitalization the same way.  Perhaps we
        should.
                 DR. DiMARCO:  Ralph?
                 DR. D'AGOSTINO:  I would like to ask some
        questions, trying to make a judgment from the presentation
        we just had and what I see in the review.  For example, in
        study 223 with the phase 2, there were three primary
        endpoints in phase 1.  One of them I guess was
        statistically significant, the other one clearly wasn't,
        and the third one was sort of marginal, which would bump
        up.  But then there's the phase 2 that comes in, where
        there is this mortality and morbidity.  
                 I think it's very important to get a sense of
        what we think about that level of significance that's
        produced.  Would you let it go as it stands, or are you
        suggesting that it should be --
                 DR. STOCKBRIDGE:  I have a great deal of
        trouble finding the words in the protocol that identify a
        long-term endpoint for this trial.  And that is the only
        document that we have had, we have seen, that addresses
        what the endpoints in that trial might be.  I believe that
        the Australia-New Zealand group had an interest in
        monitoring safety through an extended period during that
        trial, apparently for the purpose of considering a
        definitive trial later on.
                 I think that if there had been a potential
        basis for approval in a primary endpoint that was
        identified from the short-term phase, I think they would
        have been horrified to have had that taken away from them
        because of some adjustment for multiple endpoints,
        including the long-term phase.  I don't think that was what
        their intent was at all.
                 DR. D'AGOSTINO:  Can I ask a couple more
        questions?  
                 In study 240, where the combined endpoint was
        quite significant, the significance that's falling apart if
        you remove the medication, in particular, when you look at
        just straight mortality, this CHF mortality, you only have
        4 versus 0 deaths.
                 I guess I'd like some sort of statement about
        or some discussion about how one should look at that
        medication.  I started off understanding that 240 was a
        study which everybody thought was quite nice, and the more
        I looked at it, the more problems I had with it.  I'd like
        to hear your view on that.
                 DR. STOCKBRIDGE:  The FDA reviewers never did
        an analysis that was exactly the same as what the sponsor
        did.  In the first place, the only analyses we did were
        time-to-first-event.  The original protocol called for an
        analysis that just simply counted events.  The original
        protocol called for components of that endpoint which were
        cause-specific mortality, and cause-specific
        hospitalization.  The FDA reviewers never looked at cause-specific hospitalization or cause-specific mortality.
                 What we analyzed was all-cause mortality and
        all-cause hospitalization in that, and however you do that,
        it is still true that the p value floats up by a factor of
        about 10 if you drop the medications component.
                 DR. DiMARCO:  Dr. Borer?
                 DR. BORER:  You raised what sounds to me like
        sort of a critical point a couple of minutes ago, and I
        guess we'll need a response from the company about this. 
        But if indeed the purpose of counting deaths and
        hospitalizations for 18 to 24 months was to monitor safety
        and be able to make a safety statement, rather than to do
        an analysis for efficacy, the importance -- I hesitate to
        use the word "significance" because I think it's wrong
        here, but the importance of any conclusions based on that
        analysis would lose a great deal to me I think.
                 Once you said it, it reminded me of one of the
        slides, describing study 220, where we were told that
        mortality was a prespecified endpoint.  But it was actually
        prespecified as a safety assessment.  I'm sure it was
        prespecified that deaths were going to be counted to make
        sure the drug was safe, but that's different from a
        prespecified efficacy endpoint that you build an analysis
        around.
                 DR. STOCKBRIDGE:  None of the U.S. trials have
        a protocol that specifies mortality or mortality plus all-cause hospitalization, some combination of those, as a
        primary or secondary endpoint.
                 DR. BORER:  The point I was making was that it
        does sound as if there's some similarity between the
        prespecification of mortality as a safety issue in one of
        the U.S. trials and perhaps the intent to look at mortality
        and morbidity in 223 as a safety issue.  I'd want to know
        from the company whether that's what was done.
                 DR. PACKER:  Jeff, the investigators made clear
        that their intent was to look at a reduction in the
        combined risk of morbidity and mortality.  That was made
        clear not only in the original protocol but also made clear
        in the January 1995 decision to go forward with the long-term phase.  Remember, the protocol specifically said that
        unless something bad happened on the physiologic and
        clinical endpoint, that they would make a decision to go
        long-term. 
                 At that time they said that they were going
        long-term to look for a reduction in morbidity and
        mortality.  It never looked at any of the data and so they
        were actually going for this.
                 Now, their desire was to do a mortality trial,
        not to do a morbidity/mortality trial.  They were doing a
        morbidity/mortality trial to hopefully get someone to say
        they were going to do a mortality trial.  
                 So, the protocol says that their hopes are
        eventually to do a mortality trial, but what they
        prespecified was the hypothesis that carvedilol would
        reduce the combined risk of morbidity and mortality. 
        There's actually a considerable amount of correspondence
        and material in writing to indicate that.
                 DR. DiMARCO:  Do both Dr. Temple and Dr.
        Lipicky want to make comments?
                 DR. TEMPLE:  To some extent this is, I think,
        being made more complicated than it needs to be.  It's
        perfectly obvious by now that there is nothing in the
        protocol for the 223 study that nicely, neatly says, my
        primary endpoint for the second phase is X.  If there were,
        we wouldn't have had to be discussing it so long.
                 I think what the company is arguing, that you
        can deduce what it was from these various things, from the
        statement in the publication and so on.  
                 My guess is it's not going to get any better
        than that and you sort of have to decide whether you
        believe that's persuasive or not because the usual kind of
        statement just isn't going to be there.
                 But I was interested in knowing why Dr.
        Stockbridge particularly thought that they were doing it to
        find out if it was lethal because the phrases that were up
        there didn't seem to be saying that, but you might have
        some other reason for thinking that.
                 Before you answer, it's important -- probably
        everybody knows this already but I want to be sure -- to
        distinguish between an endpoint that includes death and a
        mortality endpoint.  It's very clear that there was no
        mortality endpoint in the U.S. trials, but there were
        endpoints that included one or another kind of death along
        with other things.  So, it's not that death was
        uninteresting.  It's that they weren't trials to find a
        mortality endpoint specifically.
                 Then the third thing that's worth noting is,
        they tended to look at cause-specific stuff and we tended
        to ask them not to because we're suspicious of the ability
        to classify things properly.  So, both endpoints were shown
        and you can try to decide what that means.  But they were
        looking for some secondary endpoints at some of these
        mortality/morbidity things in trials.
                 But before Dr. Stockbridge goes away, I think
        it's important to pin down what in there would make one
        think that they really weren't looking for a benefit at all
        because that would be very troublesome.
                 DR. LIPICKY:  Norman can answer that, but I
        would like to also, since opinion was asked for.  
                 I know that during our discussions with the
        sponsor setting up the development program, the only
        interest was to show there was no adverse effect on
        mortality.  That is the only thing we ever talked about. 
        That there was to be an expected beneficial effect on
        mortality was not in the cards.  It was to get a point
        estimate to show that symptoms would be better in some
        fashion and there would be no adverse effect on mortality,
        or not a very large one.
                 I guess I could have planted that idea in
        Norman's mind.
                 The second part of it is, as you read through
        the protocol, boy, if anyone can read through that 223
        protocol and come to the opinion that there was hypothesis-testing going on looking for a benefit, they've got a
        really good imagination.  
                 So, then you put that together and you say,
        well, they're interested in seeing what happens long-term.
                 I have a question to ask.  Those letters that
        were shown up here, when were they written?  After the
        study was completed, before the analyses?
                 DR. SHUSTERMAN:  The letter I quoted was
        written and communicated to us when these results came out
        in The Lancet, which is in the last week.  But the same
        statements are in The Lancet publication.             
                 DR. LIPICKY:  That's fine.  
                 So, the first that anybody knew anything that
        was even close to some written-down intent was after The
        Lancet publication was published?
                 DR. PACKER:  That's not true, Ray.  These were
        specifically outlined in the investigator's publication in
        January 1995, when they completed the analysis of the
        short-term phase, and in that publication said that not
        having any adverse effect in the short-term phase, as
        specified in the original protocol, the investigators are
        now continuing the trial for the main objective of looking
        at the hypothesis that carvedilol reduces morbidity and
        mortality.  That was in January of 1995, before any blind
        for morbidity and mortality was broken.
                 DR. LIPICKY:  Only the short-term part.  Is
        that right?
                 DR. PACKER:  Right.  And the investigators were
        not privy to any information about morbid or mortal events
        that occurred in the study.
                 DR. DiMARCO:  Cindy?
                 DR. GRINES:  I've been reviewing this protocol,
        and it mentions twice in the protocol that they actually
        propose to perform a mortality trial if there's any
        plausible moderate treatment benefits.  So, I can't tell
        from this protocol that they were expecting to see an
        increase in mortality because it's twice mentioned that
        they wanted to eventually do a large mortality trial.
                 DR. LIPICKY:  I would like to add one more
        comment to the opinion business.
                 I think we missed in our first review the
        importance of the run-in period and how that might
        influence things, and I'm differing a little bit with what
        Dr. Stockbridge said in that I think we missed this run-in
        business because the major attention was paid to the post-randomization process.  We were not convinced that it was
        an effective therapy on the basis of post-randomization
        analyses, so we didn't look for much more from the vantage
        point of what would the design of the trials mean for
        approvability.
                 DR. KONSTAM:  So, what's your feeling about it
        now?
                 DR. LIPICKY:  Well, I think we missed it and I
        certainly am thinking about it for the first time.
                 DR. KONSTAM:  Based on the data that you've
        seen.
                 DR. SHUSTERMAN:  Regarding the run-in phase,
        could we have backup slide 3 please because I think this is
        germane to this discussion.
                 DR. PACKER:  There are actually two backup
        slides.  That's the first one.
                 It's not unusual to have trials that have run-in phases.  In fact, I think such run-in phases have been
        actually advocated by FDA.  An example of a trial that has
        a run-in phase, for example, is the SOLVD treatment trial. 
        What we did in this slide was just to compare on the left
        the run-in events corrected for time in the SOLVD treatment
        arm with the run-in events in the U.S. carvedilol arm.  As
        you can see, the event rates during these two periods are
        pretty similar to each other.
                 As Dr. Stockbridge has emphasized, he didn't
        see any evidence for an excessive increase in the events
        during this run-in period.  This diagram would confirm his
        impression.  He didn't find any excess after randomization. 
        The event rate during the run-in was similar to the event
        rate post-randomization.
                 DR. LIPICKY:  Are you talking about deaths?
                 DR. PACKER:  I'm talking about deaths.
                 DR. LIPICKY:  There were very few deaths.  So,
        the fact that someone couldn't find anything in the run-in
        phase is no big surprise.
                 DR. PACKER:  Deaths are pretty serious.
                 DR. LIPICKY:  But there weren't very many.  The
        number were not very many.
                 DR. PACKER:  Well, that's because there was --
                 DR. LIPICKY:  So, if you look at it per trial,
        you will not --
                 DR. PACKER:  No, no.  This is not per trial. 
        This is for the entire program.
                 DR. LIPICKY:  What did Dr. Stockbridge say?
                 DR. PACKER:  Sorry?
                 DR. LIPICKY:  You were commenting on Dr.
        Stockbridge's comment, and was his comment on all of the
        data in all of the trials or was it a trial-by-trial
        comment?
                 DR. PACKER:  I guess we would have to ask him.
                 DR. STOCKBRIDGE:  I suppose I could have pulled
        out the primary review and looked at this again, but I
        didn't.  
                 I believe that what we looked at in terms of
        the run-in period was the mortality in the U.S. experience,
        the four major trials.  We looked at all of the deaths that
        occurred during those few weeks.
                 DR. LIPICKY:  And that was a total of 12?
                 DR. STOCKBRIDGE:  Yes.  Well, it was something
        like that.
                 DR. PACKER:  It was seven events.
                 DR. LIPICKY:  And you didn't find anything in
        that signal, and that means something?  Come on.
                 DR. PACKER:  Ray, what can you find without a
        control group?  What is findable in the absence of a
        control group?
                 DR. LIPICKY:  Nothing but you were saying we
        didn't find anything, and I'm just trying to emphasize the
        fact that that was a non-statement.
                 DR. PACKER:  But it's quoting Dr. Stockbridge's
        statement of a few minutes ago.
                 DR. MOYE:  But you can bound it.  It sounded
        like that if you assumed the worst case --
                 DR. PACKER:  Can we have the next slide please?
                 DR. MOYE:  -- then the p value still winds up
        being fairly small.
                 DR. CALIFF:  Don't leave the slide yet.
                 DR. MOYE:  Now, if the concern is not mortality
        but morbidity and mortality, what then happens?
                 DR. CALIFF:  Can I just make a comment about
        this slide?  I'm not as convinced as Milton yet.  Again, I
        just want to keep pushing the worst case here to set that
        boundary, but the underlying mortality in the carvedilol
        trials is about half of what it is in the SOLVD trial.  So,
        one would expect the run-in phase mortality to be lower I
        would think.
                 In addition, we've already learned I think that
        the U.S. experience had a lower run-in mortality than the
        trials that have been excluded.  As you said, Milton, there
        were four in your study and the New Zealand had another two
        deaths.  
                 So, I think we need to see all the data from
        all the studies, and this doesn't, to me at least, provide
        a convincing case that there's not -- it's convincing
        there's not a huge problem.  It's not a lethal problem. 
        It's not a terrible problem, but I think it is an issue
        that needs to be sorted out.
                 DR. PACKER:  Rob, in the spirit of being most
        conservative, let me just say that it is true that you
        might expect perhaps the event rate to be lower if
        carvedilol was exerting an effect.  But remember, this run-in period, this 2, 3, 4 weeks, the carvedilol curves don't
        separate for 3 to 6 months.  So, you're not going to see a
        beneficial reduction in a run-in period of only 2 to 3
        weeks in duration.
                 DR. SHUSTERMAN:  And they only received the
        lowest dose.
                 DR. PACKER:  And they only received the lowest
        dose during this period of time.
                 DR. CALIFF:  I'm making a very different point
        which is that the underlying mortality in the -- it's a
        lower risk population at a lower risk of death, and
        therefore in the run-in phase, you would expect .25 or .20
        or something to be consistent with what you see in the rest
        of the trial.
                 DR. PACKER:  Why would that be?
                 DR. CALIFF:  Because you have patients with a 5
        percent risk of dying at 6 months compared to patients with
        a 10 percent risk of dying at 6 months.
                 DR. PACKER:  Rob, if I can focus your attention
        on the bottom of this slide.  The actual event rate at 6
        months in the U.S. carvedilol/placebo arm -- and don't
        forget almost all of these patients, more than 95 percent,
        were getting ACE inhibitors.  It's exactly what was
        observed in the SOLVD treatment arm when patients were
        getting an ACE inhibitor.  So, in fact, the evidence is
        rather striking that these patients are a similar risk.
                 DR. KONSTAM:  But it's a little lower than in
        the SOLVD placebo arm, which is what Rob is saying.  It is
        a different baseline population, and it may well be that
        it's different because they're on ACE inhibitors.  So, it
        is a little bit different.
                 But, Rob, I think the magnitude of this is real
        small.  If it's 7 deaths, okay.  So, maybe it's a couple
        one way or the other.  I think the issue really is what's
        the worst case scenario and the worst case scenario is that
        all 7 deaths go over to carvedilol.  I guess that's the
        analysis that we saw.
                 DR. PACKER:  Can I have the next slide? 
                 Rob, this is the best we can do to address your
        request in the short period of time available.  This shows
        the five multi-center trials.  You can see the deaths in
        run-in and then the deaths after randomization.  Placebo is
        on the left and carvedilol is on the right.  I think you
        can feel comfortable that if you took all of the deaths in
        the run-in period, the difference between 9.9 -- these are
        crude ratios.  Please forgive us.  These are not time-to-first-event analyses.  If you took the .55 carried over to
        carvedilol, I'm not certain we would be having much of an
        impact on the delta in mortality.
                 I agree that it would be important, Lem, to
        look at this for mortality and hospitalization.  It's just
        not possible to do that right this minute.  It's easy to
        get the mortality data.  It's hard to get the
        hospitalization data.
                 DR. DiMARCO:  Dr. Roden, did you have a
        question?
                 DR. RODEN:  I had a couple of questions.
                 One is perhaps to Dr. Lipicky and Dr. Temple. 
        I've seen the list of questions, but I want to know what it
        is we're being asked.  Are we being asked to decide whether
        carvedilol reduces mortality, or are we being asked whether
        it's a useful drug in the treatment of patients with heart
        failure?  So, that's one question.
                 Then the other question I had for Milton or
        someone over there, and that is mortality is easy. 
        Hospitalization seems to me a very, very mushy endpoint
        depending on physician preferences.  I'd like some sense of
        how you think those kinds of decisions were made and
        whether it is conceivable that because these patients are
        part of a trial in which endpoints were desirable, that
        there's a bias toward increasing the number of
        hospitalizations.
                 DR. PACKER:  It's very hard to address that
        last question because I would like to think that the
        patients who are in a trial -- and I think you would share
        this view -- in general tend to get a much more vigilant
        type of care than patients who are not in a trial.  This is
        regardless of whether they get placebo or active therapy.
                 DR. RODEN:  Well, hospitalization as a sort of
        endpoint may change the way people approach that.
                 DR. PACKER:  No, I understand.  I think that in
        general when one looks at either mortality or combined risk
        of morbidity and mortality, in general the event rates are
        lower than the trial predicts.  There are lots of reasons
        why.  It's a lower risk patient population, or perhaps
        because investigators really are more vigilant.  So, in
        general, the hospitalization rates are lower than expected
        because of that.  It's hard to distinguish between that and
        other factors that you might identify.
                 There's no doubt that the most unbiased,
        clinically important endpoint in the measurement of heart
        failure -- and by the way, measurement of any disease -- is
        mortality.  But I think that ranking right underneath that
        is mortality and morbidity.  
                 That has certain advantages.  One is it tells
        you a little bit more about what the drug is doing to the
        progression of the disease because hospitalization is an
        intermediate endpoint.  Two, hospitalization is easy to
        quantify.  It's objective. 
                 DR. RODEN:  So you say.
                 DR. PACKER:  Three, biases hopefully should be
        randomizable out between placebo and active therapy.  I
        share Ralph's concern about cause specificity which is why
        just a week ago I emphasized in an editorial in the New
        England Journal that one really needs to focus on all-cause
        mortality and all-cause hospitalization as a combined
        endpoint because that gives you the highest degree of
        comfort that what you're looking at is is not subject to
        biases.  It is right underneath mortality as the most
        important thing you can measure in heart failure.
                 DR. DiMARCO:  Dr. Temple?
                 DR. PACKER:  And by the way, that's why the
        analysis on carvedilol on all-cause mortality and all
        hospitalizations across studies is so important.
                 DR. TEMPLE:  Just a little history and theory. 
        We've certainly accepted reduction in cardiovascular
        hospitalization rates as a legitimate endpoint.  That's
        what SOLVD Prevention showed.  
                 We've said repeatedly that it's cleaner and
        easier to understand if you look at all-cause anything, but
        that doesn't mean that it's not sometimes reasonable to
        look at cause-specific events.  What you have to do is
        protect yourself against bias and make sure there's an
        independent group that's blinded that makes the
        interpretations.  It would be I think a real stretch to say
        that one mustn't do that, however.
                 But I wanted to go back to the previous
        discussion.  Dr. Stockbridge was initially satisfied that
        nothing funny was going on in the pre-randomization period
        by looking at overall rates.  Dr. Califf has raised the
        question that there's a simpler way to do this and a more
        conservative way to look at this by simply attributing all
        of those events to the drug even though they happened
        before randomization.  We will obviously eventually be able
        to see that.
                 I want to be sure we understand what point is
        being made because we've looked at both pre-randomization
        deaths and pre-randomization deaths plus hospitalizations.
                 The main endpoint on which the company is
        hoping, at least potentially, to rely is not the deaths. 
        It's the deaths plus hospitalizations.  So, if one wants to
        look at the robustness of that finding, then it's the death
        plus hospitalization issue that needs to be looked at, and
        they have apparently done that for the U.S. multi-center
        studies, but that leaves some things out and it shouldn't
        be very difficult, even if they can't do it right now, to
        get the rest of those data.  
                 So, do I understand that that's the main
        question that's being raised?  You'd like to see an
        analysis that conservatively attributes all of those to the
        drug as if none of them would have happened in a placebo
        group.  Is that correct?
                 DR. CALIFF:  That's my question.  It may not
        reflect anybody else's interest.
                 DR. MOYE:  I agree.  I think that's critical
        here.
                 DR. TEMPLE:  There is a second question and
        it's important.  We know from the CAST, for example, which
        used a screening period and had lots of deaths during the
        pre-randomization period, that at least for moricizine the
        action was all in the pre-randomization period.  The
        mortality attributed to the drug was all in the screening
        period, and by the time you got into the screening period,
        it wasn't nearly as bad to be on moricizine because you had
        killed off all the susceptibles.  
                 So, looking for excess deaths, people
        hypersensitive to a beta-blocker, is also a reasonable
        question, but my impression is that what Dr. Stockbridge
        did reassured him on that question that people were not
        dying at a terrible rate during that period.  
                 So, I just wanted to be sure I got the two
        questions separated and know what everybody wants to find
        out.
                 DR. DiMARCO:  Dr. Konstam?
                 DR. KONSTAM:  I'd like to ask two questions. 
        I'd like to ask Milton, and maybe other people in the
        audience who were investigators could comment on it too.
                 Following up Dan's point with regard to
        potential bias, I'm a little concerned about heart rate
        effects, and I think that hospitalization is subjective in
        the sense that it requires a decision by the clinician, as
        certainly does change in medication.  I know if I have a
        patient whose heart rate is 110, I'm much more likely to be
        worried about that patient than somebody whose heart rate
        is 80.  It's one of the things that consciously or
        unconsciously goes into my mind as a clinician.
                 I wonder if you can comment on the likelihood
        that that biased these endpoints that required subjective
        judgment.
                 DR. PACKER:  Well, that question, I think the
        issue of potential bias comes up with any beta-blocker for
        any indication other than mortality.  Taken to an extreme
        -- and I know you're not suggesting that -- you would say
        that the only endpoint you would believe in a beta-blocker
        trial would be mortality because any other endpoint could
        conceivably be influenced by a physician who may be
        influenced by what he sees as a change in heart rate.
                 What's gratifying about what you see in the
        carvedilol program, for reasons that are not clear, is that
        in the analyses that have been done to date on a variety of
        endpoints -- and I don't think it has been done on
        hospitalization, by the way -- there doesn't appear to be
        any difference in the delta heart rate in the patients who
        had or did not have an event.  In other words, it wasn't as
        if the investigators systematically hospitalized all the
        patients with high heart rates.
                 DR. DiMARCO:  I think what Marv was saying is
        that if the patient presents with worsening heart failure
        and a high heart rate, they're more likely to be
        hospitalized because they may appear sicker.
                 DR. PACKER:  I think, John, there's a
        likelihood that the bias would have been in the opposite
        direction because if an investigator could determine what
        the patient was on by looking at their heart rates -- and
        there's evidence from these trials that they could not
        determine who was on placebo or carvedilol by an individual
        measurement of heart rate.  So, let me emphasize that.  But
        if they could, they might be more likely to hospitalize
        someone who they thought was on a beta-blocker.
                 DR. KONSTAM:  I was thinking pretty much what
        John said, that I don't think it's so much an issue to me
        of the investigator guessing what they're on as much as
        that heart rate per se is one of the things that good
        clinicians -- that enters into their decisionmaking
        consciously or unconsciously.  I'm a little concerned about
        that as a bias in the data set.
                 DR. WEBER:  But you're saying, Milton, that in
        fact did not place.
                 DR. PACKER:  That did not take place.
                 DR. DiMARCO:  What I'd like to do now is I'd
        like to just -- I'm sorry.
                 DR. LIPICKY:  Can I respond to Dan's question
        about what the questions are about?
                 DR. DiMARCO:  Surely.
                 DR. LIPICKY:  I think I'll lead you through the
        heuristic that's in the questions.  It starts out posing
        that one usually likes to think of having two trials that
        meet their primary endpoints and that the p value from that
        is .05 squared.  That's the degree of certainty that one
        would like to have that this is generalizable, it will
        happen in the patient population, so on and so forth.
                 So, the questions start out saying can you come
        to that conclusion from primary endpoints.  If you can,
        then that becomes the indication.  If from the primary
        endpoints one can say mortality and hospitalizations
        decrease on carvedilol, that is an indication.
                 Well, one might not be able to or one might be
        able to.  If you can't, then you can look at the secondary
        endpoints, create a similar circumstance where you are
        convinced that secondary endpoints have been affected to
        the degree that you would like to have for approvability,
        then you have an indication.
                 Now, then you might say, well, you might not be
        able to do that.  So, then you can take retrospective
        endpoints.  Every time you take this step, there's clearly
        an inference problem, and there are clear judgment
        problems, and there are clear penalties you pay.  And you
        are asked to define them.  So, you may be able to look at
        retrospectively defined endpoints and say, I know what this
        drug does.  That is the indication.  
                 Then you are given the opportunity in the very
        last question of saying, I can't make up my mind like that
        but it's got to be good for something.
                 (Laughter.)
                 DR. LIPICKY:  And you get to vote on that.
                 DR. DiMARCO:  Is that a suggestion we should
        move on to the questions, Ray?
                 Are there any other members of the panel who
        would like to ask questions directly of the sponsor?  Marv?
                 DR. KONSTAM:  There was one other question I
        wanted to direct to Dr. Stockbridge.  I still wasn't quite
        clear what you were saying about protocol 240.  You did a
        different set of analyses than the sponsor did.  Was your
        conclusion was not still that it reached this primary
        endpoint regardless of how you did the analysis?
                 DR. STOCKBRIDGE:  The analysis that we did had
        a p value for study 240 of less than .05.  Is that the
        question you asked me?
                 DR. KONSTAM:  Yes, I guess so.  So, it met its
        primary endpoint any way you looked at it.
                 DR. STOCKBRIDGE:  Well, again, what we looked
        at was not exactly the same as what the protocol-specified
        endpoint was.  What we looked at included all-cause
        hospitalization.  It included rather than cardiovascular
        hospitalization.  It included all-cause death not cause-specific death.  So, in that sense, what we analyzed was
        not the primary endpoint.
                 DR. KONSTAM:  Now I'm more confused.  If it was
        looked at from the perspective of the primary endpoint, it
        also reached it.  Is that not right?  That's correct.
                 DR. COLUCCI:  Bill Colucci again.
                 It should be perfectly clear, if it isn't
        already, the primary prespecified endpoints which were
        quite cause-specific were strongly positive.
                 DR. KONSTAM:  Right.
                 DR. COLUCCI:  More conservative analyses done
        by the FDA were also significant.  And reduction of the
        components of one, two -- leaving any single component --
        all of those were also positive whether by cause-specific
        or cause-nonspecific analysis.  So, I've seen no analysis
        of that study of any kind that was ever not statistically
        significant.
                 DR. STOCKBRIDGE:  If you leave out the
        medications component from either the sponsor's analysis or
        the FDA analysis which has no cause-specific component to
        it, the p value goes up by a factor of 10 in both those
        cases.
                 DR. KONSTAM:  Right.
                 DR. KONSTAM:  But it's still .05.
                 DR. STOCKBRIDGE:  Well, the FDA analysis
        started with a p value of .04 and went to .4.
                 DR. MOYE:  Right, but leaving out the
        medications is not per protocol.
                 DR. STOCKBRIDGE:  That's true.
                 DR. MOYE:  The per protocol included the
        medications.
                 DR. STOCKBRIDGE:  You're absolutely right.
                 DR. KONSTAM:  Any interpretation of the primary
        endpoint was reached.  There's no debate it reaching its
        primary endpoint.  I just want to understand.
                 DR. MOYE:  Now, the strength comes from the
        medications presumably, but the endpoint prespecified
        included the meds.
                 DR. KONSTAM:  The strength comes from the
        medications by Dr. Stockbridge's analysis but --
                 DR. LIPICKY:  No.  By anybody's.
                 DR. KONSTAM:  I said it wrong.  It falls away
        from significant value if the analysis is done according to
        Dr. Stockbridge's analysis which was not the per protocol
        analysis.  So, if you go per protocol and you take away the
        medications, it's still sticks to --
                 DR. D'AGOSTINO:  But, you know, we've been
        making a big discussion about ignoring the primary outcome. 
        This is one case where the primary outcome did in fact turn
        out to produce significance.  We probably don't want to
        wander too much away from that.
                 (Laughter.)
                 DR. DiMARCO:  Any other comments from the
        panel?
                 (No response.)
                 DR. DiMARCO:  Let's get started with the
        questions then.  Question 1.1 is, study 240 had a primary
        endpoint of time to the first event of sudden death, death
        from progression of heart failure, hospitalization for
        worsening heart failure, or sustained increase in a
        specified group of heart failure drugs.  Elimination of the
        medications component of the endpoint from either the
        sponsor's analysis, which included cause-specific mortality
        and hospitalization, or the reviewers' analysis, which
        included all-cause mortality and hospitalization, greatly
        increases the p value from 0.003 to 0.029 and from 0.04 to
        0.378, respectively, suggesting that most of the
        statistical power lies in the medications component. 
                 What effect does this observation have on the
        clinical interpretation of the results of study 240?
                 Rob, do you want to start off?
                 DR. CALIFF:  Well, I think this gets deep into
        the heart of the philosophy of determining health effects
        of a treatment.  It's one thing to say that the drug has a
        mechanism of action that improves a component of a person's
        health.  It's another to say that you improve the overall
        health state of the individual or of the population.  I
        think it's not nearly as strong when you have a change in
        the p value that's so substantial when you move away from
        the cause-specific events.  I think it's a point of
        weakness that's fairly substantial.
                 DR. DiMARCO:  Ralph, would you like to comment?
                 DR. D'AGOSTINO:  I always like to make clinical
        statements.
                 I just think that the study 240 -- somehow or
        other, we have to take it on its grounds.  It had a
        protocol.  It had a primary event.  I think it is driven by
        the medication component.  It weakens the sort of
        statistical power and so forth, but nonetheless it still,
        on their groups, maintains the significance.  So, I think
        if we play statistical significance, I think we still have
        a result here.  It certainly does weaken it clinically,
        though.
                 DR. DiMARCO:  Jeff, I'll ask you.
                 DR. BORER:  Yes, I agree with that.  Certainly
        eliminating the medications component weakens the strength
        of the conclusions and the degree of consistency of the
        data, but nonetheless, the study, as it was set out to be
        done, achieved the goal that it set out to achieve.  It
        proved the hypothesis it tried to test.
                 In addition, from what I've read here and from
        what I've heard, every other kind of analysis that could be
        done of these data still comes up with a statistically
        significant result in favor of the drug.  Now, of course,
        not all that overwhelmingly strong, but still statistically
        significant.  I'd like to see some confirmation from a
        second trial, but I would accept this as a positive trial.
                 DR. DiMARCO:  Would anyone else like to comment
        on this question?
                 DR. CALIFF:  Just one more little emphasis. 
        The big change is not taking away the drug effect or the
        effect of counting the change in medication.  The big
        change is going from cause-specific to all-cause.  Is it
        right that we should be looking for overall health effects
        that cause specific outcomes?  Do you really care if you
        die from heart failure or from something else?
                 DR. BORER:  No.  I agree with you about looking
        at all-cause.  I'm sorry.  That's quite right.  But even if
        you do that, still the overall analysis of all-cause
        hospitalization and all-cause mortality together is, as I
        understand it, statistically significant.
                 DR. CALIFF:  No.  I think it's .378.
                 DR. DiMARCO:  That's the one that goes to .378.
                 DR. CALIFF:  I think it's a great cause-specific answer to a question about how the drug works, but
        as far as the overall health effect -- that's why I say it
        concerns me that the p value goes all the way to .38 when
        you count all-cause.  If it just changed a little bit, I'd
        be more comfortable.
                 DR. DiMARCO:  Dr. Temple?
                 DR. TEMPLE:  Can someone remind me?  If you do
        all-cause mortality plus all-cause hospitalization plus the
        medications, what's the result of that?  Because that's
        what we are really talking about here.  It's the morbidity
        plus mortality endpoint that changes if you go to all-cause, but what happens if you keep the endpoint as planned
        but modify it in that way?  Does anybody know?
                 DR. PACKER:  Bob, that analysis hasn't been
        done, but based on the magnitude of the effect on all-cause
        mortality and all hospitalization, plus the medications --
        and remember, it's a 2 to 1 randomization at 50 percent
        lower risk.  I have to emphasize this hasn't been done, but
        you're combining two components which go very strongly in
        the same direction.  It's very likely that that will be
        statistically significant even when the original primary
        endpoint of 240 is broadened in a non-cause-specific
        fashion.  Of course, now that the committee has asked for
        that analysis, it can be done.
                 DR. TEMPLE:  Given that the results are largely
        driven by the medication, it seems likely that it's going
        to come out that way.
                 DR. STOCKBRIDGE:  If I understood your question
        correctly, that is the analysis that the FDA reviewers did. 
        It was non-cause-specific plus the medications.  That gave
        you a p value of .04.
                 DR. TEMPLE:  Okay, but that was on a very much
        reduced data set because you didn't find most of the
        medication data adequate.
                 DR. STOCKBRIDGE:  All of that is certainly
        true.
                 DR. TEMPLE:  I was just trying to distinguish
        between two points that are being made.  One, as Ralph
        said, for better or worse, you live with roughly the
        endpoints that they chose because we're not supposed to go
        flipping away from endpoints any more than they are.  And
        if you do that and stick with the medication, it really
        turns out not to matter very much whether you use cause-specific or non-cause-specific because that's not the major
        driver of that endpoint.  So, it's not surprising.  
                 It just means that what you've got here is an
        endpoint that is mostly about worsening heart failure as
        measured by medication use.  It's not really a
        mortality/morbidity, in some other sense, endpoint.  It's a
        more limited endpoint.  You have to decide whether that's
        clinically relevant or meaningful.
                 DR. KONSTAM:  John?
                 DR. DiMARCO:  Marv?
                 DR. KONSTAM:  I think you could approach this
        question from two different perspectives:  a statistical
        perspective and a clinical perspective.  
                 From the statistical perspective, I think you
        have to give this trial its due, as Dr. Temple was saying,
        and as we go to beat up on other trials, as we'll come to,
        that don't reach their primary endpoint, this one does and
        we got to stick with that.
                 From the clinical perspective, Rob, I am
        somewhat concerned, but I guess I'm not as concerned as you
        sound to be about the change in the p values from the
        medication difference when you take away the medications. 
        The p value rises in large part because the number of
        events is falling, but in fact the other two contributors
        are still going in the same direction for one point.  And
        for another point, it seems to me to be consistent with
        other things in the data set.  So, although it's obviously
        a big driver to the magnitude of the p value and I'm a
        little bit worried about it, I'm not that worried about it.
                 DR. CALIFF:  But again, I'm responding less to
        that than to the change from .04 to .378 which makes me
        wonder if there's an excess of non-cardiac hospital
        admissions in the carvedilol.
                 DR. COLUCCI:  I think that Dr. Konstam's point
        is very important.  That study was empowered based on
        estimates of the event rate for the three-component
        endpoint so that it really is not empowered to see anything
        when you take one of those away, particularly the one that
        is the major contributor.
                 I think it is fair to go to a non-cause-specific death and hospitalization, but really to take away
        medications really just under-powers it tremendously.  It
        was prospectively designed to be empowered to this
        endpoint.
                 The other thing to be said is that although
        medications have traditionally not been quantified in big
        clinical trials, they generally show up as an increase or a
        decrease.  This study had really the first and most
        specific criteria for change in medications of any trial
        that has been done so far.  That required a 50 percent
        increase that was sustained for over 30 days or the
        addition of a new additional drug.  
                 So, these are much more firm objective
        endpoints for change in medication than have been used in
        the past and I think are much less susceptible to the type
        of criticism that is very justified because, after all,
        diuretics are adjusted up and down, a little here and
        there.  But these are substantial changes that are
        maintained for a substantial period of time.
                 DR. DiMARCO:  Dr. Raehl?
                 DR. RAEHL:  I think you just answered my
        question, but to clarify, the change in medication to which
        we're referring is primarily due to diuretic regimen
        changes.  Correct?
                 DR. COLUCCI:  Or ACE inhibitors.
                 DR. RAEHL:  There seems to be disagreement
        among your --
                 DR. COLUCCI:  The majority of changes were
        diuretics.  The majority were diuretics that were changed,
        but it could have also been --
                 DR. RAEHL:  Is that data anywhere in our review
        that we could actually see how the medication profiles, if
        you will, changed on an aggregate basis, that being a
        primary driver?
                 DR. COLUCCI:  I believe that's available.
                 DR. SHUSTERMAN:  We don't have it here, but I
        would agree with Dr. Colucci, probably diuretics are about
        a half --
                 DR. DiMARCO:  You have to use the microphone
        please.
                 DR. SHUSTERMAN:  It also included changes in
        nitrates, changes in ACE inhibitors which made up the other
        half.  There were no changes in digoxin --
                 DR. RAEHL:  So, the criteria was a 50 percent
        increase in any of those medications, but about half of the
        time it was about a 50 percent or more increase in
        diuretics.  Is that fair to say?
                 DR. SHUSTERMAN:  Or the addition of a new
        diuretic.  Correct, yes.
                 DR. COLUCCI:  It had to be at least a 50
        percent increase in dose or a 50 percent increase in dose
        of an ACE inhibitor or nitrate or other vasodilator.  About
        half of the time, that was the diuretic.  The rest of the
        drugs contributed to the other half.
                 DR. DiMARCO:  Are there any comments with
        regard to question 1.1?
                 (No response.)
                 DR. DiMARCO:  Let's move on to number 1.2.  We
        are now moving to study 223.  What clinical benefit was the
        primary endpoint in the short-term phase?  Rob?
                 DR. CALIFF:  My reading of the short-term phase
        is we didn't have any evidence of substantial clinical
        benefit.  We had ejection fraction and ventricular diameter
        measurements that were improved.  The primary clinical
        endpoint was not affected.  Those are nice and very
        stimulating endpoints, but not measuring clinical status.
                 DR. DiMARCO:  So, you would conclude that there
        was no real demonstrated clinical benefit in the short-term
        phase.
                 DR. CALIFF:  If our goal is to understand
        overall health benefits to the patients or populations,
        there were none demonstrated.
                 DR. DiMARCO:  Ralph, any comments?
                 DR. D'AGOSTINO:  I agree with that.
                 DR. DiMARCO:  Anyone on the committee have a
        different opinion?
                 DR. GRINES:  I don't remember that that data
        was shown to us other than symptomatic data, just some of
        the negative exercise data.  But wasn't there a change in
        ejection fraction?  And we saw no symptomatic data.  So, to
        determine clinical benefit short-term would be very
        difficult.
                 DR. CALIFF:  All right, but the primary
        endpoint of clinical benefit was the exercise endpoint. 
        Ejection fraction was definitely improved, but that's not a
        patient-oriented endpoint.
                 DR. DiMARCO:  So, I think that we can move on
        to 1.2.2.  Here the question is, what clinical benefit was
        the primary endpoint in the long-term phase?
                 DR. CALIFF:  I think we reviewed that ad
        nauseam here.  The wording is not specific.  The analyses
        have been done in a variety of ways, and probably by the
        way we have come to as preferred way in this group, it's
        marginal at .04 but it's there.
                 DR. D'AGOSTINO:  I think that the protocol is
        quite deficient in flagging what the long-term is going to
        be about, and I don't see any way out of that.  If you do
        say that, well, give them the benefit of the doubt that
        this hospitalization and death that you're involved with
        there and you get a significance of .04 or .035 -- I forget
        exactly what it was -- there's still the presence of these
        other outcomes down the way, but I don't see how you can
        just disjoint this particular analysis from the fact that
        there were three other analyses going on.
                 DR. DiMARCO:  Other comments from the committee
        on that question?
                 DR. MOYE:  I just need to be sure.  Study 223
        was the Australian-New Zealand study.  Right?
                 Hopefully we want to call it a primary
        endpoint, but the long-term phase, in any event, looked at
        combined morbidity and mortality.  Is that right?  Isn't
        that right?
                 DR. D'AGOSTINO:  Yes.
                 DR. MOYE:  And the p value for that was
        provided as?
                 DR. CALIFF:  .045.
                 DR. MOYE:  Even though this was a prospectively
        designed follow-up trial, there was no prospective
        statement about what to do with these multiple
        goals/objectives.
                 DR. D'AGOSTINO:  It isn't even clear what they
        were going to do with the particular variable.  I do not
        read it that they were necessarily going to analyze it. 
        I'm not clear why it was being collected, but certainly it
        doesn't go on to your question.
                 DR. MOYE:  The result becomes even more
        skeptical.
                 DR. DiMARCO:  Following up on that, is there a
        possibility that baseline prognostic factors could to be
        used to adjust in this study?
                 DR. WEBER:  If I could ask a question.  When
        they are in fact used to adjust -- this is on slide 43 of
        the handout we've got -- the p value seems to get quite a
        bit stronger, especially when you adjust for New York Heart
        Association class and ejection fraction and so forth.  Is
        there some explanation for why that is?
                 DR. CALIFF:  I might comment on that since
        we're doing that a lot prospectively now.  It's sort of
        hard to understand why you would adjust in a randomized
        trial in the first place, but if you did it -- and I think
        Lloyd Fisher commented on this before -- in general your p
        value gets smaller because you're taking away some variance
        in the estimates.  That's about as far as my knowledge
        goes.
                 DR. D'AGOSTINO:  Or the other response to that
        is that you only see it when the p value gets smaller.  Why
        would a sponsor present it if the p value is getting
        bigger?  So, it's not clear that it will always get
        smaller.
                 DR. PACKER:  Ralph?  John, with your
        permission.  The sponsor did not propose doing any
        covariate analysis here.  It was done only in response to
        an FDA request.
                 DR. D'AGOSTINO:  I understand that.  It was
        just a comment.  I was obviously being facetious.
                 But I think the .045 is what the result that
        they wanted to produce is and we have to grapple with the
        question of whether or not we think it should be adjusted
        for multiple testing.
                 DR. DiMARCO:  Any other comments?  Dr. Temple?
                 DR. TEMPLE:  What's your answer to your own
        question?  What sort of adjustment might there be?  Well,
        there were three endpoints.
                 DR. D'AGOSTINO:  There were three endpoints. 
        No, I think --
                 DR. TEMPLE:  One of which made it.
                 DR. D'AGOSTINO:  One of which made it.  I think
        it's a good question and I don't really know the answer
        because I'm not completely convinced that one has to link
        the first with the second.  I think you might be able to
        argue -- and I was actually hoping that there would be a
        discussion -- that in fact you can separate the front piece
        from the back piece and buy power or buy alpha of .05 for
        both pieces.  I think that's a reasonable suggestion to
        make here.  So, I guess I have an opinion, but I'd really
        like to see how other people sort out that.
                 DR. TEMPLE:  That seems important because the
        thinking about this study goes in two stages.  One is can
        you decide that the second phase was designed to study
        anything in particular.  Once you get over that hump, then
        you have to figure out what to do with the nominal p value
        they observed.  So, I guess I hope there's some discussion
        too.
                 DR. DiMARCO:  Dr. Borer?
                 DR. BORER:  Personally I'm relatively
        unconcerned about dissociating short-term from long-term. 
        I don't think that's intrinsically unreasonable if that's
        what you said you were going to do.  It seems as if they're
        fairly potentially self-contained analyses that have
        nothing to do with one another.  
                 But hump number 1 here is the one that I'm
        having a little trouble with.  I accept the explanation
        that Milton and the others gave about the intention of the
        investigators, but I'd feel a lot better about that if it
        were clearly stated somewhere where I could understand it
        better.  So, that's the trouble that I'm having with this.
                 If it was actually a prespecified hypothesis to
        be tested, that the combined endpoint would improve on the
        drug at 18 to 24 months, I would accept the p value as
        being important and I would say 223 corroborated 240 and
        I'd be very happy.  But I'm not sure of the intent of the
        sponsor and the investigators in doing the study.
                 DR. PACKER:  Jeff, the correspondence that
        documents this can be shared with the committee.  I think
        everyone recognizes that 223, perhaps because it was an
        investigator-initiated protocol, could have and should have
        been better written and more clear.  
                 But the written materials that the
        investigators have provided make it clear what their intent
        was, make it clear the division separated from between the
        short and long-term phase, and that they defined mortality
        and major morbidity a priori as all-cause hospitalization
        and all-cause mortality, the least biased of all the
        analyses.
                 DR. D'AGOSTINO:  I think that it really comes
        down to, in terms of our opinion as giving advice, it's not
        in the protocol.  Would we as experts in statistics and
        clinicians be willing to separate the two and would we be
        willing to let the second phase live with its .045?  I
        don't think there's any hope of getting something out of
        your correspondence.
                 DR. PACKER:  If I could add, I think everyone
        appreciates the uncertainty in the original protocol, and I
        think that was part of the motivation why the FDA asked for
        the analyses of 220 and 221.  The concept was that if one
        could find confirmation of exactly the same analysis,
        combined morbidity/mortality, not cause-specific in other
        trials in the U.S. program -- and all the trials that could
        find it were looked at.  And it was found.  It was
        retrospective.  The individual component, the morbidity
        component, was prospective.  The combined was
        retrospective.  If one could see it there and one sees it
        there with small p values, one can get additional comfort
        about the effects seen in 223.
                 DR. KONSTAM:  John?
                 DR. DiMARCO:  Marv?
                 DR. KONSTAM:  I haven't heard any viewpoint on
        the panel that this trial has any hope of standing on its
        own.  The question then is, what support, if any, does it
        give to 240?  That's obviously the question.
                 DR. D'AGOSTINO:  Can I interrupt?  I'm sorry. 
        I think it has to stand on its own to answer the question. 
        We are being asked does it stand on its own.  Am I wrong on
        that?
                 DR. TEMPLE:  Not solo, but in combination with
        the others.
                 DR. D'AGOSTINO:  No, no, but I mean the
        question that we have before us.  Do we have the
        traditional two studies?
                 DR. DiMARCO:  Two studies, yes.  This has to be
        one study that's accepted.
                 DR. KONSTAM:  Well, let me just finish my
        comment.  I think the issue to me is do I believe this
        endpoint.  Can I look at the whole data set and believe any
        endpoint?  That's what I'm grappling with.  We have a study
        that's positive and that's 240.  In my view I agree with
        you.  The study clearly doesn't stand on its own.
                 So, the issue then becomes is there any value
        in it at all to me.  I guess I have to say there is some to
        me.  
                 By the way, why doesn't it stand on its own?  I
        think all of us agree that we don't see a primary endpoint. 
        So, there's a big problem there.
                 DR. LIPICKY:  But, Marvin, you'll be able to
        say something about that when you get down the end of the
        list.
                 DR. KONSTAM:  Oh, is that right?
                 DR. LIPICKY:  Yes, because you'll be able to
        say I couldn't draw a conclusion in number 1.  You might be
        able to use it in number 2.  Well, if you can't draw a
        conclusion in number 2, you might be able to use it in
        number 3.  Well, if you can't draw a conclusion in number
        3, number 4 says can you draw any conclusions at all.
                 DR. KONSTAM:  Well, let me ask you.  The issue
        to me is, is there a primary endpoint that is met?
                 DR. LIPICKY:  Right.
                 DR. KONSTAM:  And if there is a primary
        endpoint that is met, it's in protocol 240.
                 DR. LIPICKY:  Correct.
                 DR. KONSTAM:  Then the question for me is, is
        there any corroboration for that anywhere in the data set?
                 DR. LIPICKY:  You were asked on some primary
        endpoint here, 223, and the answer is yes or no.
                 DR. KONSTAM:  Is it not possible to draw some
        corroboration regarding a primary endpoint in study A from
        another study that does not meet its primary endpoint?  Is
        that not possible?  That's what I'm asking.
                 DR. LIPICKY:  We're talking about making a
        decision here about whether we have two studies that have
        met a primary endpoint.  Okay?  So, that is the question
        under consideration.
                 Later you'll be able to say, well, maybe not
        but something happened here.  You will get the opportunity
        to answer the thing you want to address.  You need to hear,
        can you make it clean?  And either you can or can't.
                 DR. PACKER:  Ray, I just have a question again,
        with John's permission.  If I understand it, the pivotal
        question for this part, which is 1.3, is prefaced by the
        phrase "with appropriate consideration of the supporting
        evidence from primary and secondary endpoints of these and
        other clinical trials," which I think addresses Marv's
        issue directly.
                 DR. LIPICKY:  Well, he has to make a decision
        as to whether 223 satisfies the condition for saying that
        it met a primary endpoint.  If he wants to draw on other
        trials, as you want him to, he can do that.
                 DR. PACKER:  That's what your question asks him
        to do.
                 DR. WEBER:  It asks for secondary endpoints
        too.
                 DR. CALIFF:  I think we need to answer the
        technical question of whether we're accepting that there is
        a primary endpoint in 223 which is less than .05.
                 DR. DiMARCO:  That we're going to accept.
                 DR. CALIFF:  Right.  Although I'm an advocate
        of efficient trial design and trying to answer as many
        questions as you can, it's hard to accept totally unhinging
        within the same trial these four endpoints.  It's kind of
        like taking four shots off the tee and saying, I'll take my
        best and not worry about the other three. 
                 I don't think it ought to be a severe penalty
        because there are clearly sort of two things being
        addressed here.  But I think this is where even I would ask
        for a statistician's --
                 DR. D'AGOSTINO:  I could have given my opinion
        immediately, but I thought that might be inappropriate.
                 I would say, no, this doesn't make it.  I think
        that my sense that this doesn't make it on its own because
        of the questions with the four possible outcomes and so
        forth.  But we do pick up an alternative way of bringing
        this back to us with the next question.  So, to be clean, I
        think this is a no.  We can't ignore those other pieces.
                 DR. DiMARCO:  I think we've gotten to the point
        then that we can probably take a vote on 1.3 which is
        really the question we're dealing with.  Are we going to
        accept both of these as trials which stand alone
        essentially?
                 DR. D'AGOSTINO:  Well, 1.3 says, "other
        clinical trials."
                 DR. DiMARCO:  That's right.
                 And the question is, should carvedilol be
        approved for the treatment of heart failure on the basis of
        p less than 0.05 on the primary endpoints in each of two
        adequate and well-controlled studies?  And that refers to
        240 and 223.
                 DR. TEMPLE:  We need to clarify this.  The
        order of this is that first you look at individual studies
        and their primary endpoints.  Then you look at other
        endpoints, secondary endpoints, and then you go for it and
        look at anything you want to.
                 So, this is the one about primary endpoints. 
        The question here, just to be clear -- as I read it again,
        it's not perfectly clear -- is, based primarily on two
        studies that may have met fully, partly, whatever their
        primary endpoints -- and you're allowed to think about all
        the other stuff -- does this make it in the conventional
        way, the conventional way being you have two well-controlled studies that demonstrate something that they set
        out to demonstrate.  That's sort of the conventional way.
                 But we didn't want to say you couldn't even
        think about all those other things, so that's why 1.3 says,
        oh, well, you can think about those things.  But the
        primary focus here is on those two studies and what they
        showed on their primary endpoints.
                 I don't know if that helps.
                 DR. DiMARCO:  Is everybody clear on the
        question now?  Okay.
                 Ralph, do you want to start?
                 DR. D'AGOSTINO:  Well, again, I just was thrown
        an oddball there I guess because I'm still looking at the
        statement that says "supporting evidence from primary and
        secondary endpoints of these and other clinical trials."  I
        think that "other clinical trials" is very important.
                 These two studies standing on their own --
        first, 240, we voted that it makes it.  I think 223
        standing solely on its own doesn't make it, but I think
        223, in conjunction with these other analyses we've seen,
        does make it.  So, my answer is yes to this question.  I
        hope I'm reading it correctly.
                 DR. TEMPLE:  Well, Ray may want to comment too,
        but I think that's what we were asking you.  As everyone
        has said, there are things about 223 that are not perfect,
        to say the least.  On the other hand, it's not nothing, if
        I hear you.  
                 So, the question here is, well, along with that
        which is flawed and has problems and the other study and
        the other data -- now, you may want to spend some time
        discussing the other data before you give a yes, but that
        was the idea of this question.
                 Ray, do you buy all that?
                 DR. LIPICKY:  Then the decision is not being
        made on the basis of meeting the primary endpoints in two
        trials.  I must admit there's more emphasis to those words
        than probably belong in that question, and I'd like to take
        those words out.
                 DR. TEMPLE:  The reference to the other stuff.
                 DR. LIPICKY:  Because people get a chance in
        later questions to say, oh, yes, the totality of evidence
        is overwhelming.  The question that number 1 is addressing
        is can you get there from primary endpoints in two trials.
                 DR. D'AGOSTINO:  I don't want to lose the way
        this is worded.  So, somebody keep it for a later
        discussion.  If we drop that reference to other trials and
        other supporting data, I would say, no, we don't have two
        clean trials.
                 DR. TEMPLE:  Maybe that question is really part
        of 2.  I think that's what Ray is saying.
                 DR. LIPICKY:  Yes.  Those words don't belong in
        1.  It was an error to get them there.
                 DR. STOCKBRIDGE:  Could I argue that the words
        really ought to belong in 1 since I put them there?
                 (Laughter.)
                 DR. STOCKBRIDGE:  I think what one normally has
        is something better than two trials with a p of less than
        .05.  One normally has two trials with a p of less than .05
        plus secondary endpoints that help you feel good, that make
        you believe that the primary endpoint is a plausible one,
        that the primary endpoint finding is a plausible one. 
        One's confidence is usually better than is expressed by two
        trials and only one finding in each of those trials.
                 DR. D'AGOSTINO:  I hope the FDA is going to pay
        for my stay tonight because I can see I'm going to miss my
        plane.
                 (Laughter.)
                 DR. D'AGOSTINO:  The "other clinical trials" is
        the piece.  If you want to feel good about these trials and
        so forth, there are things to feel good about.  It's the
        "other clinical trials" I think that is very important in
        terms of the way I would vote.
                 DR. DiMARCO:  So, the vote is?
                 DR. D'AGOSTINO:  If we remove that phrase from
        it, it's no, these trials don't stand on their own.
                 DR. DiMARCO:  We've got some discrepants from
        our two FDA representatives here.  Does the committee want
        to take that phrase out and just say the trials have to
        stand on their own?  Maybe I'll just take a hand vote.  How
        many want to leave it the trials have to stand on their own
        at this point in this question?
                 DR. WEBER:  Why don't we do it both ways very
        quickly, John?
                 DR. DiMARCO:  Okay.
                 DR. CALIFF:  Yes.  I think it's important to be
        clear that if we're saying we're going to make an exception
        to a clear-cut standard.  So, the first question without
        the phrase.
                 DR. DiMARCO:  So, we'll vote on this both with
        and without the phrase.  The first time we'll vote without
        the phrase, so that the trials have to stand absolutely on
        their own as two independent trials with significant
        results.
                 DR. D'AGOSTINO:  No.
                 DR. BORER:  I'm sufficiently concerned about
        all the issues that have been raised about 223 that I would
        reluctantly have to say no as well if we can only consider
        those two trials.
                 DR. DiMARCO:  Cindy?
                 DR. GRINES:  I think 240 meets its endpoint. 
        It sounds like 223 probably does not, although it has
        clinical benefit.  So, I guess I would answer no to 1.3.
                 But I'd like to point out that the materials
        that we were given state that in reconsidering carvedilol,
        the committee is reminded that Federal regulations
        pertaining to approval simply call for evidence of benefit
        from clinical trials.  They specifically say that the
        regulations do not specify a p less than .05 on primary
        endpoints in two studies.  So, I think for our committee to
        be clear on that.
                 DR. DiMARCO:  Yes.  I don't think this is going
        to be the final word on whether the recommendation will be
        for approval or not.  This is just to answer this question.
                 Rob?
                 DR. CALIFF:  No.
                 DR. DiMARCO:  I'll vote yes.
                 DR. MOYE:  I think that 240 is fine, but 223 in
        my view is extremely problematic, so I say no.
                 DR. RAEHL:  No, for the same reasons.
                 DR. WEBER:  I also, I guess like everyone, have
        a little bit of a problem with 223, and this is a little
        bit of a phony vote because if you told me there was
        absolutely no other data and everything had to rise and
        fall on 240 and 223 and that was it, I'd vote yes.  But
        knowing that there's other stuff, I can have the luxury
        of --
                 (Laughter.)
                 DR. WEBER:  -- a throwaway vote, as Lem calls
        it.
                 DR. RAEHL:  That's why I jumped ahead.
                 DR. KONSTAM:  I don't see a primary endpoint in
        223, so I vote no.
                 DR. RODEN:  No.
                 DR. DiMARCO:  So, if we throw out the phrase
        "with consideration of the other trials," the committee has
        voted as we've heard.
                 What if we keep the phrase in?
                 DR. D'AGOSTINO:  There's a grab bag of these
        secondary endpoints, some of which are significant, some of
        which aren't significant, and so forth, but there is a
        direction to them.  Then there are these other bits of
        information that come from the other trials.  Nothing is
        without fault, but I think that my hearing of the
        presentation and my reading of it is that they are very
        consistent, and I would say with this other supporting
        information, I would vote yes.
                 DR. DiMARCO:  Jeff?
                 DR. BORER:  Yes, I would echo that view.  I
        think with all the problems -- and I see a lot of problems
        -- still the overall consistency through analysis after
        analysis and analysis that was specified by the sponsor and
        analyses that were asked for by the FDA, they all seemed to
        go in the same direction.  So, I would say the same thing
        as Ralph did.  I would say yes if we include everything.
                 DR. DiMARCO:  Dr. Temple, do you have a
        comment?
                 DR. TEMPLE:  As you do this, could you identify
        somewhat more specifically what's making you feel that way? 
        I ask that because in the later questions, we point out
        that there were some specified secondary endpoints like
        globals, the New York Heart, and all that.  That's one
        category of stuff.  Then there's also the mortality plus
        morbidity analyses, and that's a different category of
        stuff.  So, not to argue the point but say which of those
        or both are convincing.
                 DR. D'AGOSTINO:  I was trying to say both
        actually in my answer.  I think that the global, the New
        York categories.  To me I'm more persuaded by the mortality
        and morbidity analyses, but I do think the secondary also
        are important.
                 DR. BORER:  Yes.  That's exactly what I would
        say.  I think the consistency of the mortality and
        morbidity data are most persuasive, but it's nice when you
        see the matrix, seeing that for most of the other endpoints
        that may not even be related in terms of pathophysiology to
        the -- mortality and morbidity may not be related all that
        closely, anyway -- that even there the results all
        generally tend in the same positive direction with the
        drug.
                 DR. DiMARCO:  Cindy?
                 DR. GRINES:  I'm going to answer yes to
        question 1.3, and it's primarily based on the statistical
        reviewer's table, table 9 on page 16, where it outlines a
        lot of the different endpoints.  It seems that the majority
        of the studies showed either a trend or a significant
        difference in favor of mortality.  All showed ejection
        fraction.  Most showed improvements in New York Heart
        Association class, subjective scores, objective scores,
        progression of heart failure.  And I think it's very
        consistent throughout the trials.
                 DR. DiMARCO:  Rob?
                 DR. CALIFF:  I'll make a few comments here. 
        I'm going to say yes too, but it's kind of in the blind pig
        finds an acorn category because the primary endpoints by
        themselves don't cut it.  We end up with this sort of
        mishmash of, in all different kinds of studies, all
        different kinds of endpoints being positive.  You get the
        feeling that something good is in there.  It's not very
        directed in the way that you'd like to see it.
                 First of all, I know we're going to get to
        this, but it's good to see some actual patient assessment
        and physician assessment in a blinded way.  I think that's
        very reassuring.
                 Then the last thing.  The one contingency I
        have is I am still hung up on the run-in phase.  The
        preliminary, sort of off-the-cuff data looks good, but I'd
        like reassurance that since this was not primary,
        secondary, or even tertiary in my mind in terms of the
        global endpoint of death and all-cause hospitalization,
        that if you did the worst case analysis, you would get
        something like a p value of .01 or .001 in favor of
        treatment.  It looks like it's going to be that way, but if
        you throw in everything bad you can, make it the worst
        case, it still looks good.  Even though it wasn't looked
        for, I don't see how you can turn your back to that.  I
        think it's compelling.
                 DR. DiMARCO:  So, that's a yes.
                 DR. CALIFF:  Yes.
                 DR. DiMARCO:  My vote was earlier yes, and I
        would just say I'd continue to vote yes.  I really think
        that this part of the question is almost sort of like 1.8
        instead of question 2 because what we're talking about is
        we're accepting something less than the perfect study in
        223 because of all the other evidence which has a broad
        pattern of consistency.  So, I sort of think we're edging
        towards question 2, but again I'll vote yes.
                 DR. MOYE:  I'm going to vote no.  I think that
        the evolution of clinical trial methodology should be for
        more stringent requirements not less stringent, and I think
        that the investigators and sponsor have the resources and
        the intellectual horsepower to do things right.  I don't
        think they did things right in 223.  
                 I think that the table that was mentioned,
        table 9, is not persuasive because it comes before table 11
        which shows a great many more study endpoints and p values
        and shows positive ones as well as negative ones.  
                 In the absence of prospective statements by the
        sponsor as to how to be guided through this, I again have
        the freedom to choose a very conservative track, and the
        conservative track is concerned for the risk of a type 1
        error in the population at large.  I think looking at a
        hodgepodge of secondary endpoints makes it very likely that
        we are misleading the population at large.  
                 I can't imagine writing a label that lists a
        host of different benefits and then says, but we're
        probably wrong on at least one of them, and that's
        tantamount to what we're doing by looking at this
        collection of secondary endpoints in a very unstructured
        manner.
                 So, my vote is no.
                 DR. DiMARCO:  Mike?
                 DR. WEBER:  Well, I guess like most people I
        have shared concerns about 223, and I think as much as
        anything, it's an irritation that it took us so long to get
        to the real story of 223.  I don't think that prospectively
        before the study began, the investigators had talked about
        short-term and long-term endpoints.  I think most of us now
        have a pretty good sense of how the study evolved, and
        there's nothing wrong with how the study evolved.  We're
        all investigators.  We know how things happen and how new
        ideas come along during the course of a study.  
                 I think all of us around this table are
        experienced enough to know that those data can still be
        very helpful.  They may not be perfect.  They may not
        satisfy Dr. Moye's strict rules for clinical trials, but it
        would have been very helpful.  And it's annoying that it
        took us so long to get at it. 
                 I in fact think the data from 223 are quite
        useful.  They may not be perfect, but they're quite useful.
                 I think the point that Cindy made was
        important, that ultimately we don't have to be judges of
        the perfection of trials.  We have to be satisfied that a
        drug is efficacious and beneficial, and I think obviously
        most of us are.  
                 I'm also reassured that some of the less
        dramatic findings, the assessments by the physicians, the
        assessments by the patients, which were done blinded of
        course, went very strongly in the same direction as the
        more objective findings. 
                 So, I really have no difficulty in believing
        that carvedilol is a good drug for the treatment of
        congestive heart failure however it may ultimately be
        labeled, and I vote yes.
                 DR. RAEHL:  I'm influenced by the morbidity and
        mortality data first but also by the overall trends of some
        of the secondary factors as described in table 9, in
        particular the Heart Association classification and
        ejection fraction.  So, therefore, I'll vote yes.
                 DR. KONSTAM:  I'm going to vote yes.  To me the
        crux of the matter is this.  We have one trial with a
        positive primary endpoint and that's 240.  I guess the only
        way I can approach it then, without another primary
        endpoint that's positive, is do I believe the results of
        240, yes or no, and my answer is, yes, I do believe the
        results of 240.
                 The reason I do comes from a variety of
        different sources of information.  The first is that 223
        looks similar although it is not a primary endpoint, but I
        think there's evidence in 223 that pushes me toward
        believing 240.
                 I think there's evidence in 220 and 221 that
        pushes me toward believing the results of 240, again
        totally the result of post hoc analyses, and therefore no
        way they could stand on their own, but again they push me
        toward believing the results of 240.
                 What also pushes me toward believing the
        results of 240 is that I think there is evidence in the
        data set toward each of the individual components of 240,
        again not from any one primary endpoint, but I can't help
        being influenced by the overall direction and magnitude of
        change of the overall mortality, which is a component of
        240, and although obviously not a primary endpoint and it
        wasn't a single trial to look at it, I can't help but
        recall the overall magnitude of this non-specified
        endpoint, nevertheless a very important endpoint,
        mortality, over the whole data set, again using it to
        support the fact that I believe the components of 240.
                 Finally, I would say that I think that the
        results of 240 are believable from what else we know. 
        They're not like a Vesnarinone result, for example, that's
        out of the blue and nobody would have expected based on
        what we know about that drug or other inotropic drugs. 
        It's in the setting of sort of 20 years of thinking about
        beta-blockers and a lot of trends in similar directions
        that one can find in the literature about beta-blockers. 
        So, I guess I don't find the results of 240 a surprise.
                 So, for all of those reasons, I believe the
        result of 240 and therefore I vote yes.
                 DR. DiMARCO:  Dan?
                 DR. RODEN:  As I read this question, we're
        being asked, whether on the basis of these and other
        clinical trials, carvedilol should be approved for the
        treatment of heart failure, blah, blah, blah, having
        reached primary endpoints in two adequate and well-controlled studies.
                 Now, I agree with everything that Marvin says,
        including the Vesnarinone comment and the decades of
        experience with beta-blockers, but I for exactly that
        reason vote no.  There aren't two adequate and well-controlled trials.
                 DR. LIPICKY:  So, has anyone kept track of the
        vote?
                 DR. DiMARCO:  Yes.  The vote is 8 to 2.
                 DR. LIPICKY:  8 to 2.
                 DR. DiMARCO:  Yes.
                 DR. LIPICKY:  So, if it's 8 to 2 to approve,
        then we are done.
                 DR. DiMARCO:  Yes, because the next three
        questions all start "if not."
                 DR. LIPICKY:  Correct.
                 But before we quit, I'd like to find out two
        things so I understand the sense of the committee.
                 So, what does carvedilol do?
                 (Laughter.)
                 DR. LIPICKY:  Can someone tell me?  Should it
        be allowed to claim that it saves lives?
                 DR. KONSTAM:  We haven't discussed that.
                 DR. LIPICKY:  Should it be allowed to claim
        that it decreases the progression of heart failure? 
        Because that's what hospitalizations and so on were in the
        past, but this is all-cause hospitalization you guys
        settled on.
                 Should it be allowed to claim it makes people
        feel better?
                 And by not going through all the rest of the
        questions, we weren't ever able to get that commitment. 
        Would somebody -- anybody -- tell me what they think
        carvedilol does?
                 DR. WEBER:  Could I ask the sponsor?  You
        started out today by saying you were not seeking a
        mortality claim.  Is there something you know that we don't
        know?
                 (Laughter.)
                 DR. LIPICKY:  Yes.  It doesn't make it.
                 DR. WEBER:  I'm getting back to the questions
        Dr. Lipicky has just asked.
                 DR. LIPICKY:  You should not ask the sponsor
        anything now.  You as a committee have said approve it.  I
        want to know for what.
                 DR. KONSTAM:  Ray, based on the --
                 DR. LIPICKY:  Okay?  Tell me.  Don't base
        anything.  Just say the words.
                 DR. KONSTAM:  I want to look up the primary
        endpoint of 240 before I answer the question.
                 (Laughter.)
                 DR. LIPICKY:  Progression of heart failure, a
        combined endpoint.
                 DR. KONSTAM:  Does it say that in the protocol?
                 DR. LIPICKY:  Yes.
                 DR. KONSTAM:  Okay, then that's what I would go
        with.
                 DR. LIPICKY:  Yes.  It was combined endpoint
        progression of heart failure.
                 DR. RODEN:  I actually think symptom relief of
        heart failure.  I think hospitalization is a very tough
        endpoint to figure out what it means especially with a drug
        that can be unblinded so easily.
                 So, I think the data, as I see them, say that
        carvedilol doesn't do anything bad.  There's this decades
        of experience that Marvin has pointed out, and most of the
        studies say that there is some relief in some of those
        indices of function, some improvement in some of those
        indices of function.  Whether that's progression of
        disease, which I think is a pretty broad kind of claim, or
        relief of symptoms, which I think is a more constricted
        claim, I'll let Ray decide.
                 DR. PACKER:  Dan, don't you think
        hospitalization is harder than symptoms?  Firmer.  I don't
        mean harder -- actually harder to achieve, yes.
                 DR. RODEN:  No, and I think that
        hospitalization patterns in New Zealand may be very
        different from hospitalization patterns in Los Angeles
        compared to Des Moines, Iowa.
                 DR. PACKER:  But you're seeing it
        geographically all over the world.
                 DR. RODEN:  Well, I think the physician
        practices are different and I think clinicians approach
        patients with tachycardia differently from patients with no
        tachycardia and heart failure.  So, I think that that's
        actually less firm.
                 DR. PACKER:  I need to say that because
        hospitalization is in vogue now as a heart failure
        endpoint.
                 DR. RODEN:  I guess except in California where
        no one goes into the hospital.
                 DR. CALIFF:  Let me speak out in favor of
        hospitalization as an endpoint.  I think although there are
        clearly different rates of hospitalization in different
        societies and health care systems, the relative difference,
        if shown to be constant is very important and represents
        clearly something that's bad for the patient, which is what
        we're charged to deal with.
                 DR. KONSTAM:  What I would vote for is indices
        of morbidity.  It reduces the frequency of indices of
        morbidity. 
                 DR. LIPICKY:  The indication would be this is
        for decreasing the incidences of morbidity.
                 DR. KONSTAM:  Of indicators of morbidity.
                 DR. LIPICKY:  Indicators of morbidity in
        patients with congestive heart failure.
                 DR. KONSTAM:  That's a first cut, yes.
                 (Laughter.)
                 DR. LIPICKY:  Can anyone do better than that?
                 DR. DiMARCO:  I would go actually what the
        endpoints in the trial were which are complications of
        congestive heart failure -- 
                 DR. LIPICKY:  But what were they?
                 DR. DiMARCO:  -- which include death,
        hospitalization, and --
                 DR. LIPICKY:  So, they get a mortality claim.
                 DR. CALIFF:  No, it's not a mortality claim. 
        It's a composite claim that includes mortality.
                 DR. LIPICKY:  Death is in there, though.
                 DR. DiMARCO:  Death is in there because that's
        what we voted.
                 DR. KONSTAM:  It's a little confusing if you
        say it that way, though, because it sounds like we're
        saying there's an effect on mortality.  I would say that
        mortality is an indicator of morbidity.
                 (Laughter.)
                 DR. WEBER:  You'll get no argument from anyone
        on that.
                 But a number of the trials used the combined
        morbidity and mortality endpoint, and it was significant. 
        How are you going to separate them out?
                 DR. LIPICKY:  All right, I understand.  So,
        that clarified it a little bit, well enough so that we'll
        be able to argue.
                 Then I'd like the committee to argue with me
        when I assert that.  What you all said was if you don't
        make it with your primary endpoints, root around in your
        data and find retrospective endpoints that sound good and
        you can wow us.
                 DR. KONSTAM:  No.
                 DR. LIPICKY:  No.
                 DR. KONSTAM:  Not at all.
                 DR. LIPICKY:  Well, how did you make that
        decision?
                 DR. KONSTAM:  Well, I already told you.  The
        issue is that we have a primary endpoint that's positive,
        and getting back to the discussion --
                 DR. LIPICKY:  One trial.
                 DR. KONSTAM:  Right, exactly.
                 And getting back to the discussion from this
        morning, I guess the only thing I'd feel comfortable
        commenting on is whether or not I believe it based on the
        entire --
                 DR. LIPICKY:  One trial?
                 DR. KONSTAM:  That's right.  Do I believe that
        that finding in that trial is positive or not?  I do feel
        that I believe the result of that trial based on many other
        things in the data set.
                 DR. LIPICKY:  So, you believe the results of
        study 240 based on seven other trials.
                 DR. KONSTAM:  I could go through it again.
                 DR. LIPICKY:  Well, that's what there are,
        seven other trials.
                 DR. KONSTAM:  Specific elements of those
        trials.
                 DR. LIPICKY:  But your conclusion that those
        other trials support 240 is because there were some p
        values for totally retrospectively defined endpoints.
                 DR. TEMPLE:  Ray, that's incorrect and you
        mustn't keep saying that.  Most of those endpoints were
        prospective.  They were just secondary.
                 DR. LIPICKY:  Which ones?
                 DR. TEMPLE:  Which ones were secondary?  Death,
        global --
                 DR. LIPICKY:  This is mortality and all-cause
        hospitalization.  You invented that endpoint yourself.
                 (Laughter.)
                 DR. TEMPLE:  Yes.
                 DR. LIPICKY:  Okay.  There's no question that
        it's retrospective.
                 DR. TEMPLE:  Ray, if you want them to use their
        official secondary endpoint which is cause-specific, they
        win on that too. 
                 DR. LIPICKY:  That was not a secondary endpoint
        in any protocol.  It was also a made-up endpoint.
                 DR. TEMPLE:  This committee told us several
        things and it's perfectly clear to me what they told us. 
        They said they do not agree that just because you fail on
        your primary endpoint, you can never learn anything from
        your secondary endpoints.
                 DR. LIPICKY:  I --
                 DR. TEMPLE:  I'd like to finish.
                 DR. LIPICKY:  But --
                 DR. TEMPLE:  I want to finish.  Thank you.
                 (Laughter.)
                 DR. TEMPLE:  They told us that.  They were very
        clear on it.
                 They also said that there were certain kinds of
        other endpoints, like the combination of all-cause
        mortality and morbidity, that are so persuasive in this
        setting that they're even willing to believe that.  Now,
        that's debatable.  Everybody can argue about that.
                 DR. LIPICKY:  That's fine.  
                 DR. TEMPLE:  But that's what they told us.
                 DR. LIPICKY:  I just want to be sure that I
        understood them that retrospective endpoints that never
        were stated anywhere at all are perfectly okay.
                 DR. KONSTAM:  As an element of corroboration.
                 DR. LIPICKY:  No, this isn't corroboration.
        This replaces a trial.  You have a trial and you're trying
        to make up a second.  Is that not what corroboration is? 
        How do you verify?
                 DR. KONSTAM:  No.  Again, the only question I
        keep asking myself is do I believe the result of that one
        trial that is clearly positive.
                 DR. LIPICKY:  And you do that by?
                 DR. KONSTAM:  Well, I'm using the word
        "corroboration."  The question is, do you need another
        positive primary endpoint in order to say that?  And I'm
        saying no.  I believe that without another primary
        endpoint.
                 DR. LIPICKY:  Fine, but you said that more than
        that, that you could make up the endpoint.  We need to be
        certain that we understand exactly what you think.
                 DR. KONSTAM:  Yes.  I think in some cases --
                 DR. CALIFF:  Ray, it sounds to me like there
        are a variety of different reasons why people were swayed. 
        In my case it actually was -- I think you're close to being
        right, but it's just that the endpoint that, as you say,
        was "made up" is the big one.  It's something that's, at
        least in my mind, impossible to ignore if it's
        overwhelming, even if you weren't looking for it, even if
        you didn't think you were going to find it.  
                 And it's there in study after study.  You put
        them all together.  It's still there.  If you count in the
        deaths in the run-in phase, it's still there.
                 DR. LIPICKY:  We would have gotten into all of
        this if you hadn't answered the first question yes.  How do
        you know it's there?  Because what you've done --
        understand what you have done.  
                 For primary endpoints it's pretty clear what
        you're doing.  Two .05's is .025 squared.
                 Now you get into the secondary endpoint
        business because the primary endpoints don't get you to the
        level of confidence you want.  What are the p values you
        need for the secondary endpoints?  At least they were
        mentioned.  Certainly you're not talking .05 anymore. 
        You're elevating these guys to some status that is
        different from what a secondary endpoint is.  You're out of
        this .05 stuff, and I would have liked to have seen what
        you thought was significant and at what level you thought
        it was significant.
                 Now even if it's a big-deal, retrospective
        endpoint, you're really elevating that guy to something
        enormous, of enormous status.  It is the same as a primary
        endpoint for purposes of approvability.
                 What p value tells you that it's there study
        after study?
                 DR. CALIFF:  Actually I think this is a very
        important point.  We might be sharper on it tomorrow, but
        certainly in monitoring clinical trials -- and I think
        somebody may have said this in one of the briefing
        documents -- when you hit a p value of .001 for all-cause
        mortality, for example, that's kind of my choking point to
        say it's kind of hard to ignore this and you may be
        crossing the boundary of acceptable continuation of not
        giving people this treatment.
                 DR. LIPICKY:  How many of those did you see?
                 DR. CALIFF:  You remember I specifically said
        in a worst case analysis, better than .001 for death or
        death and all-cause hospitalization would do it for me
        regardless.
                 DR. LIPICKY:  Well, but your comment was that
        -- and we accept your recommendation.  I'm just trying to
        understand the basis of it.  Okay?
                 Your statement was that it was always there,
        and what I see are p values that go from .002 looking
        across the sponsor's thing -- so for one study .026, .035,
        and .378.  This is for mortality and all-cause
        hospitalization.  That's your big-deal endpoint.  That's
        the nominal p values, uncorrected for anything including
        multiplicity and having been retrospective.
                 DR. CALIFF:  Those were for individual studies.
                 DR. LIPICKY:  You made the statement that it's
        really there, you really think it's there a lot, and I'm
        wondering how you made that decision.
                 DR. KONSTAM:  Just following up on what Rob
        said, I guess the single thing in the data set that makes
        me feel most comfortable that 240 is correct is the overall
        survival data. 
                 Now, then you ask the question, what kind of
        statistical correction would you do to that survival data
        given the fact that it's not a specified endpoint?  I have
        no idea how to answer that from a mathematical viewpoint.
                 DR. LIPICKY:  So, you are saying you're
        comfortable with 240 for different reasons than Rob said he
        was comfortable with 240.
                 DR. KONSTAM:  I thought he said the same thing.
                 DR. LIPICKY:  No.  He said it was mortality and
        all-cause hospitalization.  You're saying mortality.
                 DR. CALIFF:  No.  I said either one, but
        mortality being the strongest.
                 DR. LIPICKY:  The mortality being the
        strongest?
                 DR. CALIFF:  Sure.  How can you ignore it?
                 DR. LIPICKY:  We really are back to square one.
                 DR. KONSTAM:  Both.
                 DR. MOYE:  This is the trap that we fall into. 
        With no guidance from the investigators on how to interpret
        secondary endpoints, we're left with trying to root through
        this maze and it's very tough.  With eight or nine of us,
        there will be eight or nine different paths that we're
        going to take, and it's going to be almost impossible to
        build a consensus about this.
                 DR. KONSTAM:  But, Lem, just the way I look at
        it, I think mortality to me is such a big deal, and that's
        what Rob is saying.  We have this big magnitude effect with
        a very, very small p value, and I guess normally what I
        would do under that situation is turn to the statistician
        and say, what is the likelihood that that's a chance
        finding?
                 DR. MOYE:  Right, so you should.
                 DR. KONSTAM:  And I haven't gotten any guidance
        from that mathematically.  So, now I'm going back to
        saying, you know what?  It looks pretty big and it looks
        like a pretty small number.  It trends in the same
        direction in every single trial, and it's not a surprise
        from a pathophysiologic viewpoint.  To me that adds up to
        enough to be something of corroboration that the endpoint
        in 240, of which survival was an element, is real.
                 DR. DiMARCO:  Dan?
                 DR. RODEN:  I wasn't going to say anything
        more, but I feel compelled. 
                 I really feel that there is no basis for making
        a claim or including in the label the idea that this drug
        does anything to mortality.  We have criteria for
        establishing drug effects on mortality.  Those involve
        large trials.  The designs are not a secret from anybody,
        certainly not a secret from Milton.
                 (Laughter.)
                 DR. RODEN:  The notion that based on one trial
        that includes mortality as one of its many, many composite
        endpoints and then a bunch of other touchy-feely data,
        which I must say makes me feel good too, we'll approve a
        drug or we'll give it a labeling for mortality I think is
        completely inappropriate. 
                 My notion was that we feel good enough about
        this database that the drug ought to probably be approved
        for the management of symptomatic heart failure with the
        idea of reducing symptoms.  If you want a mortality claim,
        there are ways to get a mortality claim, but I really feel
        very strongly that we shouldn't entertain a mortality claim
        at all.
                 DR. WEBER:  Even, Dan, if mortality was a
        pivotal part of the data that led us to our decision and
        conclusion?
                 DR. RODEN:  It's a very small part.  Boy, it's
        a tiny part, though. 
                 DR. WEBER:  Tiny but important.
                 DR. RODEN:  There are hundreds of endpoints,
        and of those hundreds of endpoints, there are tens of
        deaths.  So, the endpoint you're talking about is
        hospitalization.  You're not talking about mortality as the
        endpoint.
                 DR. DiMARCO:  Jeff?
                 DR. BORER:  I want to make several points.
                 First of all, I think Marvin is right in his
        statement of the indication for the use of the drug, that
        it's a reduction in morbidity, the incidence of morbidity,
        whatever, because I agree that death is the worst morbid
        event you can have.  And I don't think there are data here
        that allow us to support an independent mortality claim. 
        But I do think that morbidity defined by hospitalizations,
        which I think is a pretty reasonable operational
        definition, of which mortality is the worst example, has
        been reasonably shown to be reduced by this drug.
                 Now, in terms of the supporting evidence, it's
        true, you could look at these trials and it may be correct
        to say -- I don't think it is -- well, you know, they
        looked at them with no rhyme or reason, everything is
        secondary, it's retrospective, it's this and that, and
        therefore it doesn't work.  I would suggest a slightly
        different way of looking at what we've seen here today.
                 We have a large set of data from several
        different centers, many sites, and in addition to whatever
        analyses the sponsor decided to do or the investigators
        decided to do, which maybe they did -- I don't think they
        did -- to make themselves look better, the FDA came in and
        said, well, here's this database.  We want these analyses
        done.  So, go do these.  Maybe they're different.  
                 In fact, they are different than the analyses
        that the sponsor chose to do.  They may be analyses which
        are more difficult to get a positive answer with, perhaps a
        little bit harder in terms of the type of endpoints, more
        conservative.  They're the kinds of endpoints Rob was
        talking about.
                 When those analyses were done, coming down as a
        deus ex machina out of the sky, the results are positive,
        as were the results when the sponsor did whatever analyses
        the sponsor wanted to do. 
                 I look at, for example, study 220, which I
        don't suggest by itself should stand alone as the study,
        but if we correct for 10 other endpoints that were looked
        for here, we still have a p value of p less than .02 or
        something like that.  I think that's pretty good.
                 I think that one has to look at the consistency
        of the data across the entire package we've seen.  I don't
        like the methods that we used for some of the studies.  I
        don't like some of the analyses that were done.  I share
        some of Lem's concerns about the way things were done and
        they way they shouldn't have been done.  I think all that's
        true.
                 But in the face of that, we're looking at an
        extraordinarily consistent database.  I find that
        compelling and I find it extraordinarily consistent with
        regard to what I think is a very important endpoint, and
        that is major morbidity defined by hospitalization,
        supplemented by the worst morbid event you can have which
        is death. 
                 So, for that reason, I think that the NDA
        supports the approval of the drug for that indication.
                 With regard to symptomatic heart failure, maybe
        yes, maybe no.  The data certainly trend in favor of
        symptom reduction, but I'm not totally convinced by that. 
        But at least they trend in the right way to help support my
        belief that the major morbidity is reduced.
                 DR. WEBER:  And how would you express that or
        define it, Jeff?
                 DR. BORER:  How would I define what?
                 DR. WEBER:  The indication.
                 DR. BORER:  For the reduction in major
        morbidity as measured by hospitalizations and death.
                 DR. DiMARCO:  Cindy?
                 DR. GRINES:  I'd like, I guess, to say that in
        my opinion we approve this based on study 240, and I think
        that the indication for the drug should be based on the
        primary endpoint of 240 which is a combination of death and
        progression of heart failure.  As we've all been talking,
        we're really swayed a lot by the mortality, and in 240
        mortality alone was significant.  The combined mortality
        from all these trials is highly significant. 
                 I think that it's not consistent with previous
        recommendations of this panel to just kick mortality out,
        even though that was the primary endpoint.  There are drugs
        that have been approved with combined endpoints, including
        mortality, in which there is absolutely zero difference in
        mortality, but since it was a part of the primary endpoint,
        it was included in labeling.  So, I don't know why we would
        change that in this particular study, particularly since
        most of the people on the panel are very impressed with the
        mortality differences.
                 DR. KONSTAM:  The problem with that, Cindy, is
        if you're approving it on the basis of 240 and using the
        words "morbidity" and "mortality," then it sounds like that
        it's clear to us that the drug reduces mortality.  That's
        what it sounds like.  I can't get the wording.  That's the
        problem that I have.
                 DR. GRINES:  All I know is that there are drugs
        that have been approved in just the past couple years in
        which mortality and other endpoints are in the label and
        there was zero difference in mortality, no significance
        difference whatsoever if you look at mortality
        individually.  So, why is this drug being treated
        differently?
                 DR. DiMARCO:  Dr. Temple?
                 DR. TEMPLE:  Those drugs don't have a mortality
        claim.  They have a mortality mention.  You could say that
        about aspirin, for example, which in secondary prevention
        decreases the sum of hospitalization plus death, mostly
        hospitalization, and you have to struggle to find an actual
        separate mortality claim.
                 But I guess if 240 is one of the main things
        one is relying on and really nothing else, then I'm newly
        disturbed because 240 alone, as a predominantly symptomatic
        trial, doesn't seem persuasive on its own.  What I heard
        people saying is that they find some of these other
        endpoints, whether Ray is right to say they were picked out
        of the air or not quite right, persuasive even though they
        weren't the primary endpoints of the trial because they're
        so consistent and because their p values are in many cases
        so small.  So, I heard some people say it, but that's not
        what I heard when the voting went around, that this was
        entirely based on 240.
                 It was also based on a belief that you could
        learn something from those other trials.  I have to say, if
        that's not really not true, I'm distressed by what we've
        been told because we're going to have difficulty acting on
        it I think.
                 DR. BORER:  It's true for me.
                 DR. TEMPLE:  For us to approve a claim solely
        on the basis of 240, one study in a symptomatic
        circumstance with a sort of marginal value, depending on
        how you do it, would be an unpleasant precedent for me
        personally.  But that isn't what I heard people saying.  I
        heard them saying they saw things in those other studies
        that should be considered persuasive, not perfect.  We all
        know the flaws, but that there was information from those
        studies, which were all well-controlled studies by the way,
        that meant something.
                 How to exactly write the claims I don't think
        is going to as all that actually.
                 DR. DiMARCO:  Ray?
                 DR. LIPICKY:  Well, I just want to defend
        myself for a moment.  The all-cause hospitalizations and
        mortality appeared for the first time in November of 1996
        in a letter that you wrote to them.  It never appeared
        anywhere in any protocol, any analytical plan, or any
        correspondence prior to that time.  So, if that is the
        basis of feeling comfortable, it is as retrospective as I
        can ever dream of something being retrospective.
                 DR. TEMPLE:  But, Ray, wasn't there a secondary
        endpoint in many or all of the studies --
                 DR. LIPICKY:  No, sir.
                 DR. TEMPLE:  Hold on.  I didn't finish my
        question.  I'd like to.  May I?  Do I have permission?
                 Wasn't there an endpoint of death plus
        hospitalization probably cause-specific plus increased use
        of --
                 DR. LIPICKY:  No, sir.
                 DR. TEMPLE:  Just in 240.
                 DR. LIPICKY:  Yes.
                 DR. TEMPLE:  We know that was true in 240.
                 DR. LIPICKY:  Yes.
                 DR. TEMPLE:  I'd like confirmation from the
        sponsor on that.
                 DR. LIPICKY:  Well, I copied the protocols. 
        They're in my review -- or not review -- my memo.  The
        protocols are copied exactly verbatim.  You won't find
        those words.
                 DR. TEMPLE:  You won't find all-cause, I'm sure
        of that.
                 DR. LIPICKY:  No.  You won't find a combined
        endpoint of death plus something anywhere.
                 DR. TEMPLE:  Except in 240.
                 DR. LIPICKY:  Except for 240.  That had a
        combined endpoint primary.  You will not find a combined
        anything anywhere, primary or secondary, in any other
        protocol.
                 DR. PACKER:  Ray, to be precise, each one of
        the U.S. multi-center protocols had hospitalizations for
        cardiovascular causes as its secondary endpoint.
                 DR. LIPICKY:  Death plus.
                 DR. PACKER:  Death should always be combined
        with hospitalization as a worst case.
                 DR. LIPICKY:  Terrific.  So, you just didn't
        write well.
                 All I'm saying is it is not anywhere written
        down.
                 DR. PACKER:  You can't take the worst case out
        of analysis of a non-fatal event.  You can't do that.
                 DR. LIPICKY:  All right.
                 DR. MOYE:  You shouldn't do it.  The way to
        ensure you don't is to say it prospectively.  I agree you
        shouldn't do it, but was that said?
                 DR. PACKER:  It wasn't said but the data speak
        for themselves.
                 DR. CALIFF:  I would like to just hear what Lem
        says.  How persuasive would an unexpected mortality benefit
        need to be for you?  We haven't seen what the actual
        statistical assessment is here for all the data on this
        drug.  We really actually haven't seen that today.
                 DR. MOYE:  You really missed the May meeting,
        didn't you?
                 (Laughter.)
                 DR. CALIFF:  Yes.  
                 You're saying there's no circumstance.
                 DR. MOYE:  I'm saying that the finding for
        mortality was a surprise and was not a prospectively stated
        endpoint, and that since bad surprises can occur after good
        surprises, that we should not accept the good surprise on
        its face value.  It should be confirmed in a trial done to
        look specifically at mortality as the primary endpoint and
        pushed through to the end, done in a correct way. 
                 We can learn a lot of things.  Discovery is
        fine, but you shouldn't label based on discovery I think.
                 DR. DiMARCO:  Well, are there any other
        comments from anyone on the panel?
                 (No response.)
                 DR. DiMARCO:  I think I'll adjourn the meeting. 
        Thank you all for coming.
                 (Whereupon, at 6:20 p.m., the committee was
        recessed, to reconvene at 8:30 a.m., Friday, February 28,
        1997.)