UNITED STATES OF AMERICA

P-R-O-C-E-E-D-I-N-G-S

(9:01 a.m.)

ACTING CHAIR LASKEY: Well, good morning. It being 9:00, I'd like to call us to order.

This morning we meet discussing the pre-market application for the Guidant Cardiac Resynchronization Therapy Defibrillators, P010012, Supplement 26.

And we'll begin as usual with Ms. Wood reading the conflict of interest statement.

MS. WOOD: The following announcement addresses conflict of interest issues associated with this meeting and is made a part of the record to preclude even the appearance of an impropriety. To determine if any conflict existed, the agency reviewed the submitted agenda and all financial interests reported by the committee participants.

The conflict of interest statutes prohibit special government employees from participating in matters that could affect their or their employers' financial interests. However, the agency has determined that participation of certain members and consultants, the need for whose services outweighs the potential conflict of interest involved, is in the best interest of the government.

Therefore, waivers have been granted for Drs. Jeffrey Brinker, Mitchell Krucoff, William Maisel, John Somberg, and Albert Waldo, for their interests in firms that could potentially be affected by the panel's recommendations.

The waivers for Drs. Brinker, Krucoff, Maisel, Somberg, and Waldo involve a grant to their institution for the sponsor study. The panelists had no knowledge of the funding and had no involvement in data generation or analysis. Dr. Krucoff's waiver also involves consulting for the sponsor on unrelated matters for which he receives an annual fee of less than $10,001, and consulting with a firm that has a financial interest in a competitor or unrelated matters for which he receives an annual fee of less than $10,001.

The waivers allow these individuals to participate fully in today's deliberations. Copies of these waivers may be obtained from the agency's Freedom of Information Office, Room 12A-15 of the Parklawn Building.

We would like to note for the record that the agency took into consideration other matters regarding Drs. Brinker, Krucoff, and Dr. Clyde Yancy. These panelists reported past or current interest involving firms at issue but in matters that are not related to today's agenda.

The agency has determined, therefore, that these individuals may participate fully in the panel's deliberations. The agency also would like to note that Dr. Warren Laskey has consented to serve as chair for the duration of this meeting. 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 participant should excuse him or herself from such involvement, and the exclusion will be noted for the record.

With respect to all other participants, we ask in the interest of fairness that all persons making statements or presentations disclose any current or previous financial involvement with any firm whose products they may wish to comment upon.

ACTING CHAIR LASKEY: I'd like to have the panel members introduce themselves, beginning on my right.

DR. ZUCKERMAN: Dr. Waldo, can you hear us?

DR. WALDO: Yes, I can.

DR. ZUCKERMAN: Can you introduce yourself, please?

DR. WALDO: I'm Dr. Albert Waldo from Case Western Reserve University.

DR. ZUCKERMAN: Bram Zuckerman, Director, FDA Division of Cardiovascular Devices.

DR. KATO: Norman Kato, private practice, Encino, California.

DR. YANCY: Clyde Yancy, UT Southwestern, Dallas.

DR. MAISEL: William Maisel, Cardiovascular Division, Brigham & Women's Hospital in Boston.

DR. BRINKER: Jeff Brinker, Johns Hopkins.

DR. NORMAND: Sharon-Lise Normand, Statistician, Harvard Medical School and Harvard School of Public Health.

ACTING CHAIR LASKEY: Warren Laskey. I'm an Interventional Cardiologist, the Uniformed Services University.

MS. WOOD: Geretta Wood, Executive Secretary.

DR. KRUCOFF: Mitch Krucoff, Cardiologist at Duke. I'm Director of the Cardiovascular Devices Unit at the Duke Clinical Research Institute.

DR. SOMBERG: John Somberg, Rush University.

MS. MOORE: Christine Moore, Consumer Representative.

MR. MORTON: Michael Morton. I'm the Industry Representative. I'm employed by Sorin Group.

ACTING CHAIR LASKEY: Thank you.

And, Geretta, could you please read the voting status statement.

MS. WOOD: Pursuant to the authority granted under the Medical Devices Advisory Committee charter, dated October 27, 1990, and as amended August 18, 1999, I appoint the following individuals as voting members of the Circulatory System Devices Panel for this meeting on July 28, 2004: Warren Laskey, M.D., serving as Chairperson; Norman S. Kato, M.D.; Clyde Yancy, M.D.; John C. Somberg, M.D.; Albert L. Waldo, M.D.; Jeffrey A. Brinker, M.D.

For the record, these individuals are special government employees and are consultants to this panel under the Medical Devices Advisory Committee. They have undergone the customary conflict of interest review and have reviewed the material to be considered at this meeting.

This is signed by Daniel G. Schultz, M.D., Director, Center for Devices and Radiological Health, and dated July 23, 2004.

ACTING CHAIR LASKEY: Thank you.

Before we begin the open public hearing portion, I'd like to read the following statement. Both the Food and Drug Administration and the public believe in a transparent process for information-gathering and decision-making. To ensure such transparency at the open public hearing session of the Advisory Committee meeting, FDA believes it is important to understand the context of an individual's presentation.

For this reason, FDA encourages you, the open public hearing speaker, at the beginning of your written or oral statement to advise the committee of any financial relationship that you may have with the sponsor, its product, and, if known, its direct competitors. For example, this financial information may include the sponsor's payment of your travel, lodging, or other expenses in connection with your attendance at the meeting.

Likewise, FDA encourages you at the beginning of your statement to advise the committee if you do not have any such financial relationships. If you choose not to address this issue of financial relationships at the beginning of your statement, it will not preclude you from speaking.

That being said, I'd like to ask the audience if there's anyone who wishes to address the panel on today's topic, or any other topic. If not, then I'm delighted to close the open public hearing portion and proceed with the sponsor's presentation.

DR. WALDO: Excuse me. This is Al Waldo. It's very, very hard for me to hear you.

DR. ZUCKERMAN: Okay.

DR. WALDO: I can hear you. Is that you, Bram?

DR. ZUCKERMAN: Yes.

DR. WALDO: I can hear you very well, but anyone distant from the mike is very hard for me to hear.

DR. SOMBERG: You have to put the telephone receiver near where the speaker is.

DR. ZUCKERMAN: Okay.

DR. SOMBERG: It's not going to work near the microphone. It's ‑‑

DR. ZUCKERMAN: Yes. We're about to get a better telephone. Let me check on that.

(Pause.)

MS. WOOD: We would just like to remind the sponsor to please introduce yourself and state your connection with the company and any conflict of interest that you might have.

(Pause.)

Go ahead and get set up, but we'll try to wait just a minute to make sure we can patch Dr. Waldo in where he can hear your presentation.

(Pause.)

ACTING CHAIR LASKEY: Please forgive the appearance of chaos up here. If you would, proceed.

DR. FELDMAN: Thank you.

Good morning. I'm Arthur Feldman from Jefferson Medical College in Philadelphia, and I'm very pleased to be able to be here this morning to be one of the panel that will be presenting to you data this morning from the COMPANION trial.

My conflict of interests include the fact that I'm a consultant for numerous companies, both in general cardiology and in the heart failure arena, including I received travel expenses and room and board to come here today, as well as a modest honorarium.

I was an investigator for the COMPANION trial, and I served as the co-chairman of that trial.

I'd like to begin by introducing to you the members of the trial that are here today and will be presenting to you first. First is Dr. John Boehmer who is an Associate Professor of Medicine and Surgery at the Penn State College of Medicine; Dr. Michael Bristow, who is the Gilbert Blout Professor of Medicine and co-Director of the Cardiovascular Institute at the University of Colorado; Dr. Peter Carson, who chaired the Morbidity and Mortality Committee and is Associate Professor of Medicine at Georgetown. Dr. Bristow is also the co-chair of the Steering Committee.

Dr. David DeMets, who directed the Statistical Data Analysis Center for this trial and is professor and chair of the Department of Biostatistics and Medical Informatics at the University of Wisconsin; Dr. Leslie Saxon, a member of the Steering Committee, who is Professor of Medicine and Director of Cardiac Physiology ‑‑ or Electrophysiology, excuse me, at the University of Southern California; and Dr. Jonathan Steinberg who is a member of the Morbidity and Mortality Committee and is Chief of the Division of Cardiology at Roosevelt/St. Luke's Hospital in New York.

This morning, the agenda as seen before you here, I'm going to start by reviewing some of the background for the COMPANION trial and for giving you a study overview of the COMPANION trial.

Dr. Peter Carson will then speak to data handling from the trial and the adjudication process. Dr. Michael Bristow will present the effectiveness results. Dr. David DeMets will present the statistical considerations. And then, Dr. Saxon will present the safety data and will summarize the study conclusions on behalf of the Steering Committee.

I'd like to first just preface my remarks with a little bit of the regulatory history for this trial. You can see here that the pre-IDE meeting was held in June of 1999. The FDA sent an agreement letter in September of '99, and the first patient was enrolled in this trial in January of 2000. The study was stopped on the recommendation of the Data and Safety Monitoring Committee on 11/18/02, and subsequent notices were filed with the FDA.

This next slide just makes the point that there were numerous and extensive interactions between the sponsor and the FDA during the course of this trial. These include reviewers' memos, which are found in your packets, and also systems safety communications with the approval of CONTAK CD and EASYTRAK lead systems; in May of '02, the renewal TR approval based on CONTAK TR substudy data in 104.

Next slide.

Now, I think many of you are aware of the background to this study, but I think it's worthwhile to review it in brief. I think this panel is certainly aware of the fact that heart failure is a disease of epidemic proportions in the United States affecting nearly six million people, that it's a progressive disease, and that it's characterized by very high morbidity and mortality.

Over the past two decades, a number of pharmacologic therapies have been evaluated and have proven salutory in both prolonging survival and improving outcomes in patients with this disease. However, it has been recognized now for over a decade that approximately 30 percent of patients with heart failure have a prolongation in conduction that results in a dysynchrony in cardiac contractility, and it further impairs myocardial function as well as adversely affecting the biology of the already-failing myocardium. And, unfortunately, pharmacologic agents do not address this pathophysiologic problem.

Resynchronization through electrical stimulation of both ventricles, or cardiac resynchronization therapy, has been shown to improve myocardial function, reverse ventricular remodeling, and actually improve the biology of the failing heart.

Next slide.

So how does CRT therapy work? Well, this is a diagrammatic drawing. You can see a blockage right here in the conduction system, and CRT therapy works by simply placing electrodes on the surface of the heart and then having these both ‑‑ having these timed appropriately to synchronize the contraction of the two ventricles.

Initially, about eight to nine years ago, these pacemakers were placed, or these leads were placed, on the surface of the heart using an approach through a thoracotomy. This was found to be beneficial in terms of improving cardiac hemodynamics. However, obviously, the morbidity associated with a thoracotomy was somewhat problematic in this group of patients.

More recently, leads have been developed which were used in this study, which allowed a totally percutaneous implantation by placing a lead through the coronary sinus, then down the great coronary vein, and approaching the surface of the left ventricle, with the right ventricular lead being placed consistent with standard lead placements for pacemaker devices.

Next slide.

We'll use some new terminology in the presentation that has come into the world of heart failure over the past few years. This includes CRT or cardiac resynchronization therapy. This is a generic term that describes the therapy independent of the device; CRT-P, which describes a device with biventricular pacing capabilities alone; and then, CRT-D, which describes a device with both biventricular pacing and defibrillation capabilities.

Now, we had a number of rationales for the COMPANION trial. The first was that CRT-P or CRT-D devices have the potential, because of their effects on remodeling, to reduce mortality in a heart failure hospitalization's in-patients with advanced heart failure.

Now, at the time that COMPANION was started ‑‑ in fact, up 'til today ‑‑ there have been no appropriately powered clinical trials that were designed on an intention-to-treat basis that have prospectively investigated the effect of CRT on mortality or on hospitalizations.

Now, this was important because it was really these two endpoints which were keys to understanding the efficacy of this treatment and the importance of this treatment for the heart failure population, and specifically for the heart failure physician.

Next slide.

So the COMPANION trial was designed to determine if CRT-P or CRT-D resulted in a significant reduction of a composite of time to first all-cause hospitalization or all-cause mortality when compared with optimal pharmacologic therapy alone. Combined endpoints incorporating both mortality and hospitalization are a standard for primary endpoints to receive a robust heart failure clinical trial endpoint.

The motivation behind this composite endpoint was the desire to address both mortality and morbidity. Incorporating all-cause hospitalization into a composite endpoint helps to address the challenge of competing risk and raises the bar for demonstrating effectiveness of CRT when compared to other heart failure trials.

This is the study design of the COMPANION trial. You can see that after enrollment patients underwent baseline testing. They were then randomized to one of three arms ‑‑ either to optimal pharmacologic therapy or OPT, OPT plus CRT-P, and OPT plus CRT-D.

The randomization was one to two to two, and I make this point so that you will recognize during later presentations the fact that there were twice as many patients in the OPT/CRT-D group as in the OPT group.

Another important feature of this trial was that the clock started ticking at the time of randomization. So, in other words, if an event occurred between randomization and device implant in any of these patients, that was considered as an endpoint for the trial, despite the fact that the device had not yet been implanted. So this was a very conservative approach to analysis of the trial.

A two-day window was set for implantation. The randomization was stratified, both by site and by beta blocker therapy, and the hospitalizations associated with the investigational device ‑‑ in other words, hospitalizations to implant a device ‑‑ were not considered as a study endpoint, because obviously if they were then each patient, at the time of randomization, would actually be a study endpoint.

Next slide.

I would point out also that we will concentrate today ‑‑ we will focus exclusively today ‑‑ on this OPT and CRT-D group and its comparison with OPT alone. And the reason for that was that the OPT and CRT-P data was previously supplied to the agency and was used in the approval for this device.

Now, the indications currently for a CRT-D device are seen here. They include New York Heart Association Class III or IV symptoms despite optimal pharmacologic therapy, a QRS greater than or equal to 120 milliseconds, an ejection fraction less than or equal to 35 percent, and an indication for conventional ICD.

We are proposing, based on the data that you'll see today, that these indications should be expanded to now include the same patient population ‑‑ that is, symptomatic patients with QRSs greater than or equal to 120 milliseconds and an ejection fraction of less than or equal to 35 percent, but also a current ICD indication or COMPANION patient population criteria.

Now, the composite primary endpoint for this trial was the composite of time to first all-cause hospitalization or all-cause mortality event. This composite endpoint included mortality to account for mortality as a competing risk. It was analyzed as time to first event as measured, again, from the randomization visit, not from the implantation.

The analysis was intentioned to treat from the time of randomization, and per agreement with the FDA, and in order to preserve hospitalization as a valid, morbidity clinical endpoint, the investigational device implant was not considered to be a hospitalization event.

Next slide.

So the primary endpoint consisted of a composite of death from any cause and hospitalization for any cause. However, it also included IV inotrophs or vasoactive drugs being administered for four hours in an outpatient hospital or physician office, because this was viewed as an instance of the primary endpoint with respect to hospitalization.

Now, secondary endpoints for the trial included all-cause mortality with the highest order secondary endpoint being all-cause mortality, and this was analyzed by intention to treat and it was analyzed as time to event as measured from the randomization visit, and cardiac morbidity also analyzed by intention to treat.

This slide shows the main entry criteria for the COMPANION trial. It included New York Heart Association Class III or IV symptoms, optimal pharmacologic therapy which was defined as loop diuretics, beta blockers, ACE inhibitors, and spironolactone.

Patients could be enrolled if they were found to be intolerant of these agents. However, if they were on a beta blocker or an ACE inhibitor, it needed to be at a stable dose for greater than three months in the case of beta blockers, and for greater than one month in the case of ACE inhibitors. Spironolactone also had to be at a stable dose for greater than one month.

The ejection fraction had to be less than or equal to 35 percent with a left ventricular end diastolic dimension of greater than or equal to 60 millimeters. And the QRS had to be greater than or equal to 120 milliseconds with a PR interval of greater than 150 milliseconds.

Each patient was required to have had a heart failure hospitalization between one and 12 months prior to enrollment, and there could be no indication for either a pacemaker or for an ICD.

This, again, shows the study design. Again, I'd point out that after randomization patients were randomized to one of three arms. I think it's important to also note that the patients who received the device had a hospitalization or a visit with both the physicians and the study nurse at this point, and then subsequently all patients were seen at one week, one month, and then every three months.

We made a number of statistical assumptions in establishing the goals for this trial. The trial was powered to detect a 25 percent relative reduction in 12-month event rates in each device arm versus optimal pharmacologic therapy for both the primary and the secondary all-cause mortality endpoints.

Alpha allocation was set at 0.02 for CRT-P versus OPT and at 0.03 for CRT-D versus OPT. This shows you down in the bottom part ‑‑ portion of the slide the assumed event rate for mortality or hospitalization in the control group and in terms ‑‑ and mortality endpoint in the control group, this being 24 percent mortality and 40 percent event rate for mortality or hospitalization.

This was the expected absolute reduction or the assumed absolute reduction ‑‑ 10 percent in mortality or hospitalizations, and six percent in mortality ‑‑ to give a power of greater than 90 percent for the primary endpoint and 80 percent for the mortality endpoint.

This was an event-driven trial with a target number of 1,000 first events to be detected for a 25 percent reduction for the primary endpoint. There was sequential monitoring of both the primary and the secondary all-cause mortality endpoint events performed by the DSMB every six months during the course of the trial.

Now, the management of the trial is seen on this slide, and it was independent of the sponsors. The Steering Committee was charged with providing overall guidance and leadership of the study. The Morbidity and Mortality Committee developed a process and the precise operational criteria for adjudication of the study endpoints, and then reviewed and adjudicated deaths and hospitalizations.

The Data and Safety Monitoring Board reviewed study outcomes, including safety at prescribed intervals. The independent statistical group provided statistical support as well as guidance, and the contract research organization administrated the study and acted as a clearinghouse for CRFs and study monitoring.

This shows the relationships between the various entities that were part of this study. You can see that the contract research organization received information from the independent statistical group. It gave data from patient centers to the Morbidity and Mortality Committee for their adjudication. It interacted with the sponsor.

The independent statistical group provided information to the Data and Safety Monitoring Board, who in turn made recommendations to the Steering Committee. And there was also interaction between the sponsor and the Steering Committee, and the sponsor communicated with the Food and Drug Administration.

During the context of this study, there were three occasions or approximately three occasions when there was direct interaction between components of the study outside of this diagram. First, the Morbidity and Mortality Committee communicated with the Steering Committee to clarify hospitalization as a calendar date change.

Second, the Data and Safety Monitoring Board communicated with the Food and Drug Administration regarding instances of coronary venous trauma and to provide information about changes that were made in the protocol for administration of these devices as a result of this finding.

And then, finally, the independent statistical group interacted with the Steering Committee in recommending gathering of post-withdrawal data.

Next slide.

I'd like to now turn the podium over to Dr. Peter Carson, who will discuss data handling and the adjudication process.

DR. CARSON: Thank you, Dr. Feldman.

I'm Peter Carson, and I am speaking to you this morning as the Chairman of the Morbidity and Mortality Committee of COMPANION. My conflicts are as chairman of that committee and also as a member of the panel for Guidant today. I have no other relationship to the sponsor.

The slide that is up at this point is looking at the data flow process from the standpoint of the Morbidity and Mortality Committee. A patient event that occurred would be reported on a clinical report form to the CRO, and all hospitalizations, four-hour inotrope use as an outpatient and deaths would then be assembled as a dossier and sent to the Morbidity and Mortality Committee to adjudicate.

The Morbidity and Mortality Committee then would meet in a process that I'll describe a little more later, adjudicate these events, communicate them back to the CRO, which would then further communicate them to the statistical group. There would be a final report that would then go to the sponsor.

The Morbidity and Mortality Committee communicated only with the CRO and with the Steering Committee. The Steering Committee communication was through me, and I was an ex officio member of the Steering Committee. And I would emphasize that the M&M Committee had no contact with the sponsor through the course of the trial.

Next slide.

The Morbidity and Mortality Committee was composed of seven cardiologists, and I want to take special mention of them. This was a remarkable group, and I feel like I'm a position to say so as I have chaired or been a member of virtually every Endpoint Committee in heart failure over the last 12 years. This group had great expertise in heart failure, clinical trials, regulatory experience, and also electrophysiology.

And it is well that this group had this expertise ‑‑ if we could go to the next slide ‑‑ because the committee performed a number of functions, developed the process and precise operational criteria for adjudication of study endpoints. We reviewed and adjudicated deaths and hospitalizations. For those deaths, we defined and adjudicated a mode of death, and we also adjudicated the relationship of death to device implant.

Regarding hospitalization, further, we defined and adjudicated specific causes of hospitalization. And, finally, we adjudicated cardiac morbidity.

Next slide.

In consideration of ‑‑ regarding operational definitions, some of the committee's criteria involved these thoughts. For a hospitalization event, an event should be of sufficient morbidity to enter a composite with mortality, and should also have verifiable components.

For cause-specific mortality, we assessed that the cause of death would be the event that defined the patient's clinical course or altered it, and it should be definitions that have been used in previous clinical trials.

For cause-specific hospitalizations, similarly, we wanted to indicate the primary reason for hospitalization. With evidence from specific treatment and response, we again wanted definitions that had been used in other clinical trials. I should note that, per protocol, we did not adjudicate elective implants or reimplant hospitalizations.

Next slide.

For mode of death analysis, as said, the primary mode of death related to the event that led to death. We did not usually adjudicate according to the terminal event.

We principally assessed cardiac deaths, because that's what occurred in COMPANION. The two principal causes are sudden, unexpected, and pump failure, and you see short descriptions of these modes of death on this slide. As with other parameters on this slide, fuller definitions are in the Morbidity and Mortality Committee manual.

Other causes, as you see, for cardiac deaths include ischemic deaths in two ways ‑‑ cardiac procedure, other cardiac. Vascular deaths, non-cardiac deaths. And for those cases in which there was simply no data available, these cases would be assessed as unknown or unclassifiable.

In terms of the relation of device implant to mortality, we used a schema that was typical of intervention trials ‑‑ pre-operative, after randomization but before implant; peri-operative, within 30 days; post-operative, after 30 days. We assessed the relationship as non-applicable if this was a patient in the OPT arm or a CRT-D patient who never received a device. Procedure-related and device-related were also assessed, and these details are once again in the operations manual of the committee.

For hospitalizations, let me principally say a word about heart failure hospitalizations. We were looking for a principal diagnosis of heart failure. We looked for increases signs or symptoms of heart failure. And treatment had to include intravenous therapy, either diuretic or another type of vasoactive drug, or it could be other parenteral therapy on occasion, or we also assessed its significant alteration in oral therapy could also be included in the diagnosis of a heart failure hospitalization.

We adjudicated many other causes of cardiac hospitalization. I should also add that we also adjudicated all non-cardiac hospitalizations also, and that is quite unique for any heart failure trial.

The cardiac morbidity index is seen on this slide. This is from the protocol. Please recall that hospitalization was assessed as the primary reason when we looked at it, and, therefore, one of the purposes of the cardiac morbidity scale was to pick up other morbidities that might have happened during the hospitalization or other important components of that initial reason for hospitalization.

Bear in mind that all of these aspects of cardiac morbidity would be reflecting cardiac worsening. That was their design, and that was the way the committee adjudicated them.

Next slide.

The M&M Committee adjudication process involved the CRO collating clinical summary and event information from investigational centers. This was to involve hospitalizations. It involved a calendar date change, and I'll show you the hospitalization CRF for that later. Also, outpatient IV or vasoactive drug use for greater than four hours on another CRF, and, of course, all deaths.

Please note the committee did not screen adverse experiences. All AEs in submission were reported by center, reviewed by the CRO, and submitted to the Data and Safety Monitoring Board in a summary format.

A little further detail on the adjudication process in terms of what we received from the CRO, and I should point out that the documentation in the COMPANION trial was among the best I've seen in any clinical trial I've been associated with.

This involved hospitalization data, admission summary and physical, discharge summary, lab reports, progress notes when we needed them. Death data included a physician narrative, clinic notes, and a discharge summary if the patient had had a recent previous hospitalization.

A primary and secondary reviewer were assigned to each event, and they reviewed, presented the cases to the committee, and a vote was taken for each adjudication. It should be pointed out that the patient ID, randomization arm, physician center, etcetera, were all removed from the documentation that both reviewers and the committee saw. The process for each committee meeting was documented with meeting minutes.

I should make a statement about M&M Committee blinding. I think as you probably all realize, in a device trial such as COMPANION, blinding is largely problematic. For mortality events, the committee adjudicated the relation of device and implant procedure to death, so, therefore, the committee had to be unblinded to whether the patient had a device or not.

For hospitalization events, while, as I said, all identifying data was removed to the degree possible, the nature of a hospitalization or the events themselves or statements in the narrative, even if you black them out, might reveal or hint the presence of a device.

However, please keep in mind that the committee functions in equipoise regarding the study hypothesis, and, therefore, the knowledge of the treatment arm should not interfere or influence adjudication of individual events. And the committee at no time had knowledge of cumulative events or assembled data.

Further, while CRO members were present at committee meetings, no sponsor representative was ever present, and all communication was to the CRO or to the Steering Committee.

Next slide.

Now, there has been concern about the definition of hospitalization adjudication, and just a few comments to make here. The committee believed that the protocol intended that an event be significantly or sufficiently morbid to enter into a composite endpoint with death.

It is also true that all trials prior to COMPANION had used a parameter of a 24-hour duration hospitalization. For these reasons, the committee initially used a 24-hour duration as the descriptor of an all-cause hospitalization.

Now, the largest experience in this area prior to COMPANION was MERIT heart failure and VALHeFT. In both of those trials, the committees ultimately used a descriptor of a calendar date change, and they did so for the same reasons as we did, which is that early in the adjudication process it became apparent that discharge times were not uniformly available.

Therefore, the committee agreed to adopt what was a more verifiable and precise approach of a calendar date change. This operational criteria was approved by the Steering Committee and utilized for all hospitalizations and included in all analyses.

There were 113 hospitalizations adjudicated prior to the adoption of this criteria. All were reviewed, none changed. If you look on the next slide, you see two things that are quite important. One is the flow of events through the course of the trial, noting that the first Endpoint Committee meeting was 3/16/01, and that on 1/19/01, after 113 events, we particularly used to use ‑‑ we used a calendar date change.

Then, for a hospitalization, this is the overall stream of events that occurred through the course of the trial. This is why I particularly compliment this committee. I should also say that the hospitalization CRF was in place at the start of the trial, and it was the same hospitalization CRF for the entire trial.

If you go to the next slide, this is the hospitalization CRF. What this hospitalization CRF asked the site to report was what day the patient was admitted and what day the patient was discharged. It did not ask for times. The committee did realize during the course of adjudicating that first 113 events that we could not accurately ascertain always the discharge summary.

We felt we would be vulnerable to the issue of the times, and, therefore, we felt this was clearly verifiable. Note that this form was in place at the very beginning of the trial.

Next slide.

In terms of ‑‑ Dr. Feldman talked to you about four-hour inotrope or vasoactive therapy use. We used this definition for the adjudication of these events. This is actually the wording of the definition that is out of the cardiac morbidity area of the protocol.

I should comment that four-hour endpoint of IV inotrope or vasoactive therapy use has really been the only way that this endpoint has ever been used in clinical trials, and it provides assurance that the administration of IV therapy is clinically meaningful and is a hospitalization equivalent.

Next slide.

And just like with the hospitalization CRF, this was the CRF that the sites always used that had the four-hour distinction for IV vasoactive or inotrope use. So this was also used from the beginning of the trial onward.

Next slide.

Let me conclude by saying that the COMPANION Endpoint Committee provided operational criteria for events occurring during the study. The classifications used were those used in previous clinical trials. They provided verifiable data and maximized capture of significant events.

The adjudication process consisted of activities that are the standard practice for clinical trials in heart failure.

Thank you.

ACTING CHAIR LASKEY: Thank you.

Dr. Bristow, if you would kindly indulge us for a moment, we're going to try and get Dr. Waldo back online. So can we just take a minute?

I was just told it wasn't going to take a while, so either we move ahead or ‑‑ five-minute break? Mike, is that all right?

DR. BRISTOW: Sure.

ACTING CHAIR LASKEY: All right. Five-minute break, please, and we'll ‑‑ we will regroup.

Thank you.

(Whereupon, the proceedings in the foregoing matter went off the record at 9:44 a.m. and went back on the record at 10:00 a.m.)

ACTING CHAIR LASKEY: Thank you for your indulgence. I guess we're functional, as we say. So we'll continue with Dr. Bristow's presentation.

DR. BRISTOW: Thank you, Dr. Laskey.

It's my privilege to present the effectiveness results of COMPANION. I'm Mike Bristow from the University of Colorado. I was a co-chairman of the Steering Committee. My other relevant conflicts are that I'm a consultant to Guidant, and I also receive research support to Guidant.

MS. WOOD: Sir, pull the mike up just a little.

DR. BRISTOW: The first slide is the geographic location of the study centers. This was entirely a U.S. study conducted in 120 U.S. centers averaging 12 patients enrolled per center. This gives some of the baseline demographics and other historical data in the two treatment groups.

The first point in the baseline data is that none of these parameters that we're going to be describing are different between the two treatment groups. So the age is late sixties, which is a little older than standard heart failure clinical trials that have reported lately.

We had a substantial number of women, a little higher than most heart failure clinical trials, so 67, 69 percent male. And the New York Heart Class ‑‑ all Class III and IV. This was an advanced heart failure study.

Duration of heart failure is typical for a heart failure ‑‑ chronic heart failure clinical trial, three to four years. Severe LD dysfunction, average EF, 22 percent. Dilated chrome EPI phenotype, as mandated in the protocol, was 6.7 centimeter ventricles.

Heart rate a little lower than is usually seen in heart failure clinical trials, reflecting a background therapy of beta block aid ‑‑ one of the lowest, if not the lowest, systolic blood pressure at a heart failure clinical trial reporting at least oral agents ‑‑ in this case, obviously, a device trial at 112.

Next slide.

Moderate exercise, six-minute walk, on the high side PR intervals and QRS durations based on the protocol, 55 to 60 percent ischemic typical for a heart failure trial enriched in diabetes, also typical for a heart failure trial, 45 percent. Seventy percent left bundle.

Background therapy shown here ‑‑ approximately 90 percent of patients on an ACE or an ARB, 66 or 68 percent on a beta blocker, virtually all patients on a loop diuretic, and 55 percent on spironolactone, probably representing the upper limit of tolerability of this agent in an advanced heart failure population.

This slide gives some of the details on trial termination. On November 18, 2002, the DSMB recommended to the Steering Committee that enrollment be stopped for two reasons. First and foremost, this was an event-driven trial with a target number of events of 1,000, and it was the opinion of the DSMB at that time that that target had been reached, based on the number of endpoints that they were reviewing at that time ‑‑ 941.

And then, projecting the number of endpoints that had not yet come in ‑‑ and, in fact, the final number of endpoints analyzed in COMPANION was 1,020. The second point was that the effectiveness boundaries for the primary endpoint and mortality had been crossed in the CRT-D group at that time.

So the Steering Committee followed this recommendation, stopped enrollment at 1,520 randomized patients on that date, and established a study cutoff date for gathering efficacy date as November 30, 2002.

These are the sequential monitoring Z values that the DSMB was observing over time, and you can see out here at the end of the trial the boundary for the primary endpoint being crossed.

These are the Kaplan-Meier curves for the primary endpoint, which is a composite of time to mortality or all-cause hospitalization. And the OPT or control group is in red. The interrupted line and the solid blue line is CRT-D.

The first point is that the 12-month event rate in the OPT group was 68 percent, which is somewhat higher than we had projected. In the CRT-D group, the 12-month event rate was reduced to 56 percent. That's a 12 percent absolute reduction.

The hazard ratio for these two curves is .80, statistically significant, relative risk reduction of 20 percent. Therefore, a P value adjusted for sequential monitoring ending up being .011, which is under the critical value of .03.

Now, in terms of the components of this primary endpoint, if ‑‑ taking both groups together, 90 percent of the primary endpoints were hospitalization. Seven and a half percent were mortality, approximately. And only two and a half percent were the IV inotrope use.

Next slide.

This adds on to the Kaplan-Meier curve the results in the CRT-P group for the primary endpoint. And you can see that the CRT-P group actually is virtually superimposable to the CRT-D group. In other words, the treatment effect for the primary endpoint heavily driven by hospitalization, is virtually identical in the CRT-D and CRT-P group.

Next slide.

These are some subgroup analyses, hazard ratios for standard subgroups that are looked at for the ‑‑ in heart failure trials for the primary endpoint, and the important point is that all of these point estimates lie to the left of unity, indicating homogeneity, essentially, of treatment effect for the primary endpoint.

Next slide.

This is the sequential monitoring data for the Z statistic that DSMB was following for all-cause mortality. And you can see the boundary effectiveness, boundary being crossed here at the end of the trial for mortality.

These are the Kaplan-Meier curves for the secondary endpoint of all-cause mortality. Obviously, these curves are very different. The 12-month event rate in the OPT group was 19 percent ‑‑ a little less than predicted ‑‑ down to 12 percent in the CRT-D group, absolute risk reduction of seven percent. The hazard ratio for these curves is .64. That's a 36 percent relative risk reduction, highly statistically significant P value.

Next slide.

This adds on the mortality results for the CRT-P group. And unlike for the primary endpoint, these curves are somewhat different. So this is CRT‑P, which has a hazard ratio of .76 compared to the .64 for CRT-D. And so two-thirds of the reduction in mortality in this trial was achieved in the CRT-P group compared to the CRT-D group.

Next slide.

This gives some of the subgroup analysis data for all-cause mortality. And much like the primary endpoint, the vast majority of these point estimates lie to the left of unity, indicating homogeneity of treatment effect across subgroups.

Next slide.

This is some of the death classification data from Dr. Carson's Morbidity and Mortality Committee. The majority of deaths in this study, as you would imagine, are cardiac ‑‑ around three-fourths. So here is the crude mortality rate in the OPT arm versus CRT-D, 18.8 versus 12.8 percent, statistically significant.

Here is the subdivision by the two major types of cardiac death ‑‑ adjudicated pump failure and sudden death. There are either trends or statistically significant reductions in both of these modes of death, with a greater degree of reduction perhaps, for sudden death. And here are the other more minor modes of death that were classified.

Next slide.

So this slide gives the projected event rates and treatment results based on what actually happened. So as we've already said, we projected that the primary endpoint event rate would be 40 percent at 12 months, and 24 percent for the secondary endpoint ‑‑ the event rate at 12 months, the actual ‑‑ in the OPT group.

The actual event rates achieved are shown here ‑‑ 68 percent, greater obviously, for OPT for primary endpoint, and a little bit less for all-cause mortality. So going down here to the relative reductions, we assumed that we would get 25 percent relative risk reduction, and we ‑‑ for the primary endpoint, and we ended up with 20.

We assumed 25 percent for mortality, ended up with 36. What really counts for statistical significance is a combination of the event rate and the absolute risk reduction. And in the case of the primary endpoint and mortality, the absolute risk reduction was a little greater than we anticipated ‑‑ 10 versus 12 for the primary endpoint, six versus seven for all-cause mortality.

We measured cardiac morbidity by protocol in this trial. So there was a cardiac morbidity index designed to encompass all significant events that could happen to a heart failure patient ‑‑ significant clinical events, including in this case serious device-related hospitalizations.

Now, there is no standard definition for cardiac morbidity for advanced heart failure trials. You can't reach into the bucket and pull out a standard definition for this. So the protocol defined cardiac morbidity for the COMPANION trial, and this endpoint was intended to measure frequency and duration of all cardiac morbid events as defined in the protocol.

So these are data for the aggregate of the cardiac morbidity index, in terms of frequency per patient, frequency per patient per year, and duration. OPT is in red, and CRT-D is in blue. And you can see there's a reduction in these morbidity measurements in the CRT-D group for all three of these types of measures.

And this breaks it out by component of the morbidity index. And for the ‑‑ at least for the high prevalence components of this index, there is a reduction in the CRT-D group. For example, hospitalization for a acute decompensation heart failure, you see the degree of reduction here. Statistically significant.

Next slide.

COMPANION, I'll have to say, after working in heart failure clinical trials for nearly 25 years, was a bit of a challenging study to conduct, and for that matter to design. The first sort of hurdle that had to be overcome, as we knew that we were not going to be successful with every implant, but we also wanted to conduct this as intention to treat with randomization triggering essentially the tabulation of endpoints. We didn't want to wait for successful implants and then start tabulating, which typically has been done in device trials.

We knew we had to drag along the upfront implant lack of success rate, and so in the CRT-D group the success rate was 91 percent. So right up front, we're dragging along nine percent of patients who did not get a device and could not have a treatment effect. So we have to overcome that with efficacy over time.

Another major challenge here that wasn't fully anticipated when the trial began, because I don't believe it could have been, was that there were several devices that were approved and, in fact, marketed while this trial was in progress ‑‑ several CRT devices. So a CRT-P device was approved, a CRT-D device, and there were expanded indications for ICD based on the beta trial, beta II trial, that came on the scene. And, of course, this created competition essentially for enrollment.

And so these challenges slowed enrollment and made maintaining patients in the study somewhat of a challenge. So this is enrollment by month over time in COMPANION, and you can see up until mid 2001 we're kind of zinging along here with increasing rates of enrollment. And then these devices started being approved and marketed, and this is probably no coincidence ‑‑ that our enrollment rate begins to drop.

Next slide.

So we had to have a response to that as a trial in terms of how to cope with this and deal with this. So CRT device approval while COMPANION was in progress clearly influenced investigator equipoise. Investigators were faced with the difficult choice of continuing to enroll and treat patients in COMPANION or basically put a device in them in an open label fashion or drop them into that therapy if they were COMPANION patients.

So the Steering Committee strongly discouraged that and, through direct communication with investigators, made them aware that the only way this could happen in COMPANION ‑‑ that is, a patient could get an open label drop-in device ‑‑ would be if they had progressive heart failure to the point of having a heart failure hospitalization ‑‑ in other words, would be endpointed first in COMPANION.

And the investigators were required to consult with a Steering Committee member prior to implanting device and produce on paper the evidence that this patient had progressive heart failure.

Next slide.

Nevertheless, we did experience a disproportionate withdrawal rate in COMPANION in the OPT group. And when this was first fully appreciated, early 2003, the numbers were a withdrawal rate in the OPT group, in-patients who had not previously had a primary endpoint of 13 percent, versus two percent in the CRT-D group.

The study, of course, was based on intention to treat, and due diligence in this setting requires accounting for as many patients as possible. So Dr. DeMets, the independent statistician in COMPANION, recommended to the Steering Committee to obtain vital status and hospitalization status on all of the withdrawn patients.

In order to do that and be in compliance with HIPAA regulations, we essentially had to write a new protocol and reconsent patients that had withdrawn prior to 11/30/02, who had not had a primary endpoint.

Next slide.

And so we did that, and this was a very painful process requiring a total of seven months, delaying publication of COMPANION and delaying this meeting today. So IRB-approved protocol had to occur in each center. The patients had to sign a written consent.

And, therefore, data-gathering was just as it had been in patients who had not been withdrawn. That is, case report forms for the withdrawal contact were filled out, but ‑‑ which is in addition to the standard, but also that the standard hospitalization, the CRFs were filled out, and the data were handled and adjudicated just as other data were thereafter.

Next slide.

So here is what happened in terms of withdrawals. So in terms of all patients withdrawn, 26 percent in the OPT group versus 6.6 in the CRT ‑‑ now, these are final numbers, not the preliminary numbers I showed you earlier. So in terms of patients who had not had a primary endpoint, which is the important issue, 14 percent in OPT versus 1.5 percent in CRT-D. This is prior to the reconsent process.

And so then we go through the reconsent. We end up finding these extra endpoints, identifying these extra endpoints, 14 in the OPT group, or 4.5 percent of the total, and .7 percent CRT-D. And then the real issue is: what are you left with at the end of all this?

These are the number of patients with no ascertainment ‑‑ that is, truly withdrawn, no ascertainment ‑‑ after that withdrawal, which is down to four percent in the OPT group and .7 percent in the CRT-D group. And the important number here is actually what happens in the CRT-D group, because if we missed endpoints there obviously we ‑‑ we might bias the results in favor of the therapy.

And as you can see, this number is extremely small and certainly in keeping with dropout and withdrawal rates in heart failure clinical trials that are conducted in the most rigorous manner.

Next slide.

So this is what happened in terms of withdrawals for mortality. Same numbers up here, starting with 26 and six. It ends up being 14 for patients who have had a primary ‑‑ or have not had a primary endpoint. And the bottom line is we end up with only 4.9 percent withdrawn with no ascertainment percentage for OPT, and one percent for CRT-D. And so 95 percent of patients in the OPT arm basically are followed to a conclusion.

Next slide.

And so the bottom line on this differential withdrawal is shown here. The measures taken ‑‑ an IRB-approved reconsent process, minimize the impact of withdrawals. In addition, the more complete data ‑‑ these more complete data ‑‑ that is, the data that included the withdrawal ‑‑ as it turns out were not qualitatively different from data censored at time of withdrawal.

The data really didn't change. It's just more robust. As a result, we do not believe withdrawals adversely affected the results of COMPANION.

Next.

In summary, the COMPANION patient population was well balanced across groups. There is no baseline imbalance that could explain the treatment outcomes. In COMPANION, there were statistically significant and clinically meaningful reductions in the primary endpoint of first all-cause mortality or all-cause hospitalization by 20 percent, a 36 percent reduction in all-cause mortality, and a reduction in various cardiac morbidity measurements.

And as I just said, the reconsent process we don't believe jeopardized the trial and did not create important bias.

Thank you.

Now, Dr. DeMets will present some statistical considerations.

DR. DeMETS: Thank you. I was asked by the Steering Committee to join you today to make a few comments on some of the statistical considerations that were raised in the view of COMPANION.

My primary role in this study was to serve as the independent statistician for COMPANION. That was done through a contract between Guidant and the CRO with the University of Wisconsin. That's my only financial involvement other than payment for the trip to be with you today.

So, as I said, my primary role is to support the COMPANION Data Monitoring Committee. I did have the opportunity to be involved a bit with the protocol design at the beginning, and our statistical center was the primary source of data for the New England Journal publication. Some of the analyses that we did were in fact included in the ‑‑ in your ‑‑ in the submission.

So I listed here five issues that sort of were raised to some extent during the review process, and I'm going to comment on each of them sequentially.

The issue of proportional hazards was raised, and I'd like to just make a few comments. First of all, the Kaplan-Meier curves, which are traditional ways to present time to event, did not make any assumptions about proportional hazards. And, furthermore, the proportional hazards assumption is really not required for the log rank test.

That's testing the null hypothesis. That's a well-known result in sequential literature. So that is not a requirement. There are certainly some ‑‑ certain properties where that's not required.

As a footnote, the cost proportional hazards model is ‑‑ the only covariate in treatment. In fact, it is algebraically identical to the log rank tests. So even for that particular case it's not required.

Now, the log rank test certainly has good statistical properties for something we call a stochastic ordering. To the non-statistician, one manifestation of that is that the survival curves don't cross.

So if you look at the primary endpoint, which Dr. Bristow just presented to you, the important feature here is that these two survival curves don't cross. This is for all-cause mortality and all-cause hospitalization. And the second slide ‑‑ next slide ‑‑ for all-cause mortality is ‑‑ also, they do not cross.

So with regard ‑‑ next ‑‑ with regard to the proportional hazards function, one, it's not required for the log rank test. But even so, the hazards are not drastically non-proportional. We looked at this pretty carefully, fitting models, looking at log plots.

But, in addition, the sponsor asked Dr. Kenny Larntz, who is a consultant to them, to do some further analysis looking at what he called Schoenfeld residuals, and the correlation between those residuals in time shows no correlation. So from my perspective, as an independent statistician, there really aren't any concerns about applying the log rank test to this particular set of data.

Now, we often use hazard ratios as a handy statistic to summarize treatment effect. And, of course, if it's ‑‑ if the model, as appropriate, then, is ‑‑ as I said, it's a very useful statistic. But even if the hazard ratio is not constant, the simple hazard ratio is still an average of those hazards that may perhaps be changing.

However, one could look at other summary statistics. And so relative risk at, say, one year is one particular way you could summarize the effects. So I've done that for both mortality and mortality plus hospitalization. And as you can see here, the ‑‑ whether you look at the hazard ratio or the relative risk at one year, these results don't change a whole lot.

Next.

Another sometimes common way to summarize time to event data is to look at the median time to failure, and the proper way to do that is to use the Kaplan-Meier curves and look at the 50th percentile. For this particular trial, for mortality, we don't have 50 percent mortality for the patients in this time, so you can't do that.

I'll just make the comment that you can't just simply take the observation ‑‑ observed failure times and take an average, because that methodology doesn't take into account staggered entry, censoring, and all of those aspects that are factors in real survival time in terms of event trials.

Next.

The issue of hospitalization is another important topic. In survival analysis, all of the methods that we use make a very important assumption that the censoring that we look at is independent of the risk ‑‑ underlying risk. Well, in COMPANION, clearly mortality is a competing risk for hospitalization, or for any other cause-specific hospitalization for that matter.

Thus, the rationale which is traditional in heart failure trials at this point in time, is to look at death plus all-cause hospitalization, or perhaps death plus a cause-specific. You can look at hospitalization alone, and we are often tempted to do that, but just ‑‑ you have to keep in mind that in a formal sense there is a potential for bias because of the competing risk, and that's certainly the case here in COMPANION.

Mike ‑‑ Dr. Bristow talked a little bit about the post-withdrawal events. Again here you have to look at the assumptions that we used to do the analysis. Both the log rank test and the Kaplan-Meier survival curves assume, again, that censoring is independent of the disease process.

Furthermore, intention to treat requires that all patients randomized in all events for the specified endpoint are counted. The definition is consistent with the ICH guidelines in Document E-9.

We certainly agree that COMPANION has had informative censoring due to the disproportionate withdrawal in the censoring related to the treatment arm. Therefore, if you just take the data without following the patients up post-withdrawal, you really don't have analysis that is in some sense unbiased. And in a strict sense, it's not valid.

The only solution to that problem, and one that's, again, time-honored in clinical trials, is to try to eliminate or minimize the censoring or loss to follow-up. So that requires, as I recommended to the Steering Committee at the conclusion of COMPANION, that they do everything possible to follow those patients up.

As Dr. Bristow has shown you ‑‑ next slide ‑‑ for both the primary endpoint and mortality, we started out with a number ‑‑ 80 in OPT arm and 300 in the CRT-D arm ‑‑ which was from my perspective an unacceptable high rate to leave on the table. So through the process which you described, we got that number down to the 12 in OPT and four in CRT-D.

So it's now down to a number that's ‑‑ while not perfect, it's certainly consistent with other trials. And the important point, as you said, is we have four ‑‑ potentially four patients for whom ascertainment from the time of withdrawal to the end of the study December 1st we don't know.

And for mortality, again, we whittled it down to 15 versus six. So I think that I commend the sponsor and the Steering Committee for pursuing this with the vigor it took and the time it took, but I think you need to get those numbers down to that level to eliminate any potential for uncertainty.

The issue of alpha allocation, we have two treatment arms to control here. One can divide the .05 alpha in a variety of ways. You can divide it in half. In COMPANION, it was divided .03 versus .02, reflecting the priority and the focus of most importance to the Steering Committee and to the sponsor.

It was stated in the protocol clearly, and it was in the sample size section, and it was discussed and agreed to between the sponsor and the FDA. Survival is, in this study, the leading secondary endpoint, and in some sense the ultimate endpoint for heart failure trials. It has been treated as though it had a separate alpha allocation, and this, again, was discussed and agreed when the sponsor and the FDA had their pretrial discussions.

The reason I think this is satisfactory is that mortality is a special endpoint. It's not one that's subject to interpretation, modifications, definitions. And it's the only endpoint that I would grant that special status to. So it is a secondary endpoint with its own .05 alpha, as we have interpreted and presented in the trial.

So from my perspective, the alpha allocation for death and hospitalization is appropriate, and the same is true for mortality.

The issue of subgroups ‑‑ subgroups are intriguing, but they always must be done, analyzed, and looked at cautiously. It's important to remember that subgroups must be defined properly, and by that we mean using baseline data only. However, even in this setting where we looked at baseline data, we have had problems historically in our heart failure trials.

Many of you are familiar with the PRAISE I and PRAISE II trials ‑‑ properly-defined, baseline-defined, subgroup was identify an ideology, but, in fact, it was not able to be verified in its subsequent trial in PRAISE II.

Well, why is that perhaps? Subgroups are small. The estimates are not reliable, and you expect some variation. From my perspective, you should look at subgroups with what I consider an eyeball test, general overall consistency, don't demand perfect consistency ‑‑ you shouldn't expect it. You can use it to validate previous hypotheses and perhaps generate new ones.

As Dr. Bristow showed you in COMPANION for the primary endpoint, these hazard ratios are generally pretty consistent, all showing sort of a positive effect with some variation, as you would expect.

Next.

Not only is there consistency across the subgroups, but to me what was most remarkable is that COMPANION, like other positive heart failure trials we've seen, shows a remarkable consistency across the primary and the whole portfolio of secondary endpoints, whether it's mortality or mortality plus hospitalization or cause-specific hospitalization, quality of life, life functions, and so forth.

So this kind of consistency is what we've seen in other trials that have been already alluded to such as MERIT, CIBIS-II, COPERNICUS.

To summarize, the log rank analysis is valid. Portionality hazards is not required. Stochastic ordering is really the ‑‑ was really what we really need. The bias from the informative censoring was resolved to the extent possible by the followup. I think the allocation of the alpha is appropriate. Look at subgroups, but look at them cautiously, and, as I said, the overall consistency for me was impressive and consistent with other trials that I've been involved with.

Thank you very much.

DR. SAXON: My name is Leslie Saxon. I'm from University of Southern California. My disclosures include the fact that I receive research funds from the sponsor and serve as an advisor. I own no equity.

My task today is to describe, first, the safety of CRT-D, the device used in this trial. As way of background, the CONTAK CD device or the CRT-D device used in COMPANION, and the EASYTRAK lead, have been approved in a patient population with current indications for both CRT-D therapy and an ICD. This is based on the results of the CONTAK CD study. There were no OTR or CRT-P device used in COMPANION, and EASYTRAK lead have, in addition, been approved for the COMPANION patient population based on COMPANION exercise substudy data.

Nonetheless, adverse event reporting in this trial was complete and inclusive, and adverse events were defined as any undesirable clinical event. Centers were required to report all adverse events, whether they were related to the device or not. Complications, as a subclassification of AEs, were defined as adverse events resulting in the need for invasive intervention to correct, loss of significant device function, death, or permanent disability. And this was in accordance with FDA guidelines that were established in 2000.

Observations were another category of AEs that were defined as events that were resolved non-invasively and were generally transient or reversible. While system safety evaluation in COMPANION was not predefined in the protocol, we did evaluate CRT safety according to the system safety definition, which is that system safety is defined as complications related to any of the implanted components or their ‑‑ or the associated implant procedure in those patients who were successfully implanted with the CRT-D system.

This is measured as the complication-free rate, and this has been used in previous FDA approved files, and it is measured over a six-month interval post-randomization. It is considered to be acceptable at a lower bound of 95 percent confidence interval, if the complication-free rate is greater than 70 percent.

Other safety definitions utilized in this trial and others include device safety. This is a more inclusive definition than systems safety. It includes both complications and observations related to any of the implanted components or associated implant procedures.

This was reported for all patients, randomized to CRT-D devices as opposed to system safety, which is all patients implanted. Patient-related safety is an even broader category, referring to complications or observations associated with the patient's underlying medical condition. This AE is reported for all patients randomized to CRT-D as well as those randomized to optimal pharmacologic therapy, and this excludes adverse events that are attributable to the device or the procedure.

These, then, are the system safety results. System-related complications were observed in 12.6 percent. This is of successfully implanted patients. This gives a complication-free rate of 87.4 percent with a 95 percent lower bound of 85.1 percent. Those events that occurred in greater than one percent frequency included loss of LV capture observed in 4.6 percent of patients, los of right atrial capture seen in 1.7 percent, and phrenic nerve stimulation in 1.5 percent.

The graph to the right shows the percent subsystem related complication-free rate at 87 percent, well above the lower acceptance boundary, and equal to or exceeding that of other performed CRT trials.

This slide provides the system and device safety data. As I just stated, the system safety percent of patients experiencing a system safety event were 12.6. This number increases when including the graph to the right showing device safety as it includes all patients randomized, not just successfully implanted, in terms of complications but also expands the definition to include observations listed to the right.

Patient-related safety ‑‑ the more inclusive category of all patients randomized according to the total complications and observations, are shown in this slide. That's why the numbers are somewhat higher. This would include a total of all complications and observations in the OPT group versus the CRT-D group for more serious complications, and then observations given on the right.

This table illustrates the system-related adverse events in all patients successfully implanted through ‑‑ from randomization to six months that occurred greater than one percent of the time. The columns in yellow indicate ‑‑ I would draw your attention there ‑‑ indicate those instances that required an intervention or resulted in a loss of therapy.

So while phrenic nerve stimulation was observed in 60 patients, it only required invasive intervention in three. And in one patient, it resulted in loss of therapy due to the need to turn or not to cause ‑‑ not to have LV stimulation due to persistent stimulation.

Loss of LV capture threshold was observed in 36 patients, and the majority of this did require a reintervention but was successfully resolved in all but three instances. Loss of RV capture and loss of right atrial capture were also seen and is consistent with other device trials.

Okay. The next slide indicates procedure-related adverse events in all patients randomized, and includes things such as post-surgical wound discomfort, hematomas, and coronary sinus traumas. What should be noted, again, is those that required invasive intervention or resulted in loss of therapy. Coronary sinus venous trauma did result in the need for invasive intervention in 1.2 percent of patients but did not result in loss of therapy, only an instance of device infection required, loss of therapy due to the need to remove the device.

We'd now like to address the Steering Committee's response ‑‑ we'd now like to provide the Steering Committee's responses to the FDA questions. The background to this is that the Steering Committee felt strongly that it would be helpful to the FDA to comprehensively address the reviewers' questions as part of our presentation.

The sponsor shared the FDA Director's comments with the Steering Committee, and the FDA encouraged the sponsor to address these questions through the thoughts of the Steering Committee members.

Let's start with the first question from the FDA reviewers, which relates to the hospitalization definition. Number one, please comment on whether modifications to the hospitalization definition impact the interpretation of the primary endpoint. The Steering Committee feels that the hospitalization definition has been applied consistently throughout the trial.

The original case report forms dated 1999, and submitted with the initial IDE, have the date of hospital admission and discharge and included a note of four-hour need for IV inotrope or vasoactive therapy. Therefore, the hospital data are complete, and the definition was, in fact, consistently applied for the entire study population.

Further, the primary efficacy endpoint hospitalization piece was not, in fact, modified three times or changed three times as was mentioned in one of the reviewer's comments. Rather, the primary endpoint remained the same throughout and included, again, any death, any hospitalization with a calendar date change or use of IV inotropic or vasoactive therapy lasting greater than four hours, administered in an outpatient setting, to treat decompensated heart failure.

Adjudicated events needs to have precise definitions for verification and consistencies. Endpoint Committees typically provide these definitions, and these definitions are typically, in addition, refined early in the trial as was the case after four percent of the hospitalizations were adjudicated in this trial.

Two, hospitalization definition impact. Please comment on the impact of modifications to the hospitalization definition on the interpretation of the secondary endpoint of mortality. The independent Steering Committee does not agree that the hospitalization definition was, in fact, modified. The validity of the primary endpoint definition, and, therefore, its statistical significance allow for analysis of secondary endpoints.

Further, the all-cause mortality endpoint, as Dr. DeMets suggested, represents a particularly robust outcome and has been a historical gold standard for heart failure device trials.

Three ‑‑ are the data from the COMPANION clinical trial sufficient to support an expanded patient population for the sponsor's CRT-D device? The Steering Committee feels that this was a large, multi-center clinical trial properly and rigorously conducted under the guidelines of an independent Steering Committee, Data Safety and Monitoring Board, statistical group, and Mortality and Morbidity Committee.

The trial design employed an endpoint of all-cause mortality or all-cause hospitalization. The conservative nature of this endpoint required a higher standard of clinical evidence to demonstrate effectiveness. The results are sufficient to support expanded indications as demonstrated by meeting both the primary and secondary endpoint and, in addition, demonstrating remarkably consistent, multiple relevant positive endpoints across multiple subgroups.

Four, indications for use. With respect to statements in the indication for use regarding the primary endpoint ‑‑ A) Are the data from COMPANION sufficient to support claims based on the primary endpoint results? This study demonstrated a statistically significant 20 percent reduction for the primary endpoint of all-cause hospitalization or all-cause mortality and support the claims. The secondary endpoint events were consistently adjudicated by the independent Mortality and Morbidity Committee.

B) If so, please comment on whether the language of the proposed indications for use statement adequately describes the endpoint. In particular, please discuss whether the term "all-cause hospitalization" is appropriate. We feel that the language accurately describes this endpoint. The definition of all-cause mortality is identical to that employed by the Morbidity and Mortality Committee in the adjudication process.

In addition, we feel that it is a more conservative and more comprehensive methodology than what is typically used or may be used in other heart failure trials such as a cardiovascular or heart failure hospitalization endpoint, and, importantly, is consistent with the pretrial mandate of the FDA.

Five, with respect to statements in the indication for use regarding the secondary endpoint of mortality, are the results from the COMPANION clinical trial sufficient to support a mortality benefit claim for the sponsor of CRT-D devices in the COMPANION population?

The study demonstrated a statistically significant reduction in time to all-cause mortality of 36 percent. This improvement is in addition to the benefit conferred by optimal pharmacologic therapy. Therefore, the mortality results support this indication.

Six, please comment on whether the CRT-D labeling should characterize the total number of hospitalizations and length of time patients spent in the hospital for the CRT-D and OPT arms of the companion trial. No, we do not think the labeling should reflect this, because the issue of competing risk makes analysis of hospitalization days alone problematic and inaccurate.

E) If so, please comment on whether device implant hospitalization should be included as part of that analysis. Again, no, in terms of device implantations. The FDA did approve the study design, which specifically excluded implant hospitalizations from analysis, because to do so would be to give each patient a primary endpoint event at the time that they were admitted to receive device therapy.

However, adverse events reporting occurred from the time of randomization and was comprehensive and complete, not from successful device implant as has been employed in other trials. And, therefore, all adverse events were captured and reported in the analysis. Thus, the implant hospitalization and risks are adequately addressed in the proposed labeling.

Seven, please comment on whether the CRT-D labeling should present adverse events from the CRT-D and OPT arms of the COMPANION trial in a consolidated manner that would allow their comparison. The safety of previous CRT-D devices that have been approved has traditionally been based on the system safety definition ‑‑ that is, complications related to the implanted system. It is consistent with that methodology.

The proposed summary of safety and effectiveness currently lists adverse events from both groups. The sponsor has indicated to the Steering Committee that they are willing to work with the FDA to prepare an appropriate format for accurately presenting adverse events. That is consistent with the pre-agreed investigational plan.

Eight, please comment on whether data obtained from patients after withdrawal should be used in any of the analyses described in the device labeling. Again, we emphasize that this trial was designed as an intention to treat trial. Thus, all data must be included to avoid bias. And any treatment comparison that does not include all events is not valid.

In the COMPANION trial, these efforts to complete the data set were designed, in fact, to minimize bias, due to the differential withdrawal rate observed in the OPT group. The Steering Committee felt that it was obligated to make every reasonable effort to ascertain the primary event status of the withdrawn patients.

I'd like to conclude by stating that the COMPANION study incorporated a primary endpoint of all-cause mortality and all-cause hospitalization. That is the most rigorous evaluation of CRT therapy performed to date. When added to optimal pharmacologic therapy in patients with moderate to severe heart failure, left ventricular dysfunction, and QRS delay, time to all-cause mortality or all-cause hospitalization was significantly reduced by 20 percent.

Time to all-cause mortality was significantly reduced by CRT-D therapy ‑‑ has a ratio of .64 by 36 percent.

Finally, CRT-D is safe for use in this patient population, with a safety profile similar to or exceeding that demonstrated in prior CRT-D studies performed in less advanced heart failure patients.

That concludes our comments on the Steering Committee.

ACTING CHAIR LASKEY: Thank you very much, folks. That was all-encompassing.

I'd like to, at this point, ask the panel ‑‑ we're actually right on schedule. So before we take a break at 11:00, we potentially have a few minutes up here to query the sponsor for the usual burning issues.

Dr. Brinker?

DR. BRINKER: I realize and agree with the concept that the initial hospitalization for device implant did not count against hospitalization. What I'm a little bit uncertain of is, if a patient had an unsuccessful primary implant, and had as many ‑‑ well, numerically many, maybe not proportionately many, patients had one or two or even three more implant attempts, were the subsequent implant attempts counted as hospitalizations?

DR. FELDMAN: Yes. We can actually show you the absolute numbers on that. They are important to look at ‑‑ if that's okay.

Leslie, do you want to ‑‑

DR. SAXON: In order to maintain consistency related to this concept of not primary endpoint of ND patients for devices, we, in fact, did not count the second attempt. So there were initially 15 percent of patients who were not successfully implanted. Those that were taken back included ‑‑ excuse me. I want to just look at this.

So reattempt was not done in 31. The remainder ‑‑ 50 ‑‑ were taken back for a second attempt, and that ‑‑ that was considered an index hospitalization for implant and not counted.

DR. BRINKER: I can understand from a physiologic point of view that studying the disease while you review that ‑‑ it seems to me that the impact of the second procedure has as much morbidity, if you will, associated with it, possibly more, than a four-hour hospitalization for a vasoactive drug in an emergency room. So I'm concerned a bit that the bottom line doesn't reflect that.

DR. FELDMAN: Well, I think, first of all, we're looking at endpoints not over a short window of time, which is what you're looking at with a reimplant. But in this trial we were really looking at endpoints over a very long period of time. And the two endpoints that we're most concerned with in caring for a heart failure patient is either mortality or hospitalization.

We want patients to live longer, and we want them to feel better. So I think we recognize the fact that upfront there is a certain procedural intervention that is associated either with putting the device in, or in a very small number of patients putting a device in a second intervention if you will. But over the long term we're looking at what happens to these patients, and I think that's a more appropriate comparator.

DR. BRINKER: Well, let me just take this to ‑‑ a little further. I think that a second and third and perhaps even fourth reoperation for a failed implant is not a short-term issue necessarily, number one. Number two, we are looking at single events as indices of an endpoint, in terms of hospitalization.

So one issue would be that these single events in some ways are used as surrogates for the likelihood of the patient having a worsening ‑‑ a worse clinical status that extends beyond that single event. And that's one justification for treating in a single hospitalization as an endpoint, if it got heart failure therapy, let's say, for four hours versus a second implant.

But I ‑‑ it's not absolutely clear to me that one single hospitalization for four hours of vasoactive therapy is, in fact, an issue that indicates a worsened ‑‑ prolonged worsened state of heart failure. So one question that I would ask you is: do you have any information about cumulative per patient hospitalizations?

Does one hospitalization always mean that over a period, a year or two, that these people would be repeat? Or did many of them, in fact, have only one hospitalization? And that would be equatable to a repeat surgical procedure for implant.

DR. BRISTOW: Before we address that issue, let me just add a little more comment on your first point. The patients in the OPT group who dropped in for devices, those hospitalizations, those elected an implant hospitalization also didn't count. So we consistently applied the standard that if it was an implant hospitalization, done electively, out of the context of any other reason to hospitalize, that wouldn't count, just like it ‑‑ up front, so that ‑‑

DR. BRINKER: Well, but again, I make the differentiation between a primary implant, which is ‑‑

DR. BRISTOW: Right.

DR. BRINKER: ‑‑ I agree should not be counted against it.

DR. BRISTOW: Right.

DR. BRINKER: But second and third means that there was a problem with the first, and that being assigned to that therapy imposes an additional risk.

DR. BRISTOW: Well, and that could possibly be. We'll try to comment further. But I want to make the point, shown on this slide, that an implant hospitalization is not the same thing as any other kind of hospitalization for a heart failure patient.

So this gives the duration in days of hospitalization for implants. And notice the implants in the OPT group. These are the drop-in implants around three days versus what happens with a medical hospitalization if you will, getting up close to eight days' duration.

So it's a completely different thing in terms of the impact on a patient and what it means in terms of natural history, we would argue, whether it's a device implant related or it's a real medically-driven hospitalization.

Now, in terms of what happens, if you get hospitalized once, does that set you up for subsequent hospitalizations? The answer for a heart failure patient is yes. What can we provide from COMPANION to support that? We have the multiple hospitalization backup slide.

We don't have ‑‑ we probably can't give you direct evidence that you're looking for. But as you'll see on the clustering of number of hospitalizations, there are many patients hospitalized multiple times, which is the expected ‑‑ one hospitalization begets further hospitalization. That's, in fact, why we have that as an inclusion criteria, because we know it increases the event rate for hospitalization to have a historical hospitalization by two- to threefold in fact, as well as a mortality rate.

DR. FELDMAN: While we're looking for that, let me make one other comment, and then I think Dr. Saxon wants to make a comment as well. You mentioned the fact that there were three or four attempts in patients. In fact, only three patients had a second attempt. No patients had three or four attempts, and ‑‑

DR. BRINKER: My reading of that was that ‑‑ you mean a second attempt after the first one.

DR. FELDMAN: Right. Here's the actual data.

DR. BRINKER: So that's three. That's three procedures.

DR. FELDMAN: Right.

DR. BRINKER: That's what I was referring to.

DR. FELDMAN: But that only occurred in three patients.

DR. BRINKER: Right.

DR. FELDMAN: And here is the data. So you can see that ‑‑

DR. BRINKER: But two occurred in, what, 15 percent, did you say?

DR. FELDMAN: No, no, only ‑‑ excuse me ‑‑ 8.4 percent. So here's the actual data. Here's 98.8 percent, here's the success rate for the first attempt, here's a first reattempt and the success rate, and here's the second reattempt and the success rate. But here you only see three patients, and here you only have 50 patients out of a total of 588 patients. So a very small number had to be ‑‑

DR. BRINKER: Well, in here it's eight percent had at least one more, and half a percent had at least two more. So these, as you know from watching some of these procedures, especially ones that are complicated the first time, can be long duration, high radiation exposure, a lot of other morbidity, both on the patient and the physician.

So they're not easy things, and I was just trying to equate this with the four-hour drug ‑‑ now, the fact has been brought up that the average time in the hospital for events, where it was actually quite long mean time, in the range of eight days, suggests that actually the ‑‑ suggests to me at least something that I didn't see quickly before in your data, and that is that the absolute number of ER or physician visits that resulted in a four-hour infusion made up presumably a very small number of the actual hospitalizations.

DR. BRISTOW: Yes, 2.5 percent of the total primary endpoints. 2.5 percent on the average between the two treatment arms was ‑‑ the IV was really a trivial number of events as a contributor to the primary event.

DR. FELDMAN: Leslie, do you want to comment?

DR. SAXON: Just a couple of additional comments specific to your concern related to the second first attempt. Number one, we did capture all significant morbidities that may have occurred as a result of that second attempt hospitalization. While the hospitalization didn't count against the primary endpoint, any badness or major morbidity associated with that was, in fact, counted, as was every AE that was then adjudicated by the Data Safety and Monitoring Board.

The other piece is that because we understood what this procedure involved, and I myself have implanted many of these devices, what we encouraged investigators to do in the trial was if the trial exceeded four hours, or there were issues related to difficulty in cannulating the cornerstones or one of the other technical pieces, that they feel free to bring the patient back.

So a reattempt was considered something that could occur in order to limit implant time, limit potential morbidity, and this was the consensus after looking at the early data and just with our knowledge of the procedure itself. So I think that the ‑‑ you know, to focus on that second attempt as being a potentially more morbid event is, in fact, not true in many of the cases, that we encourage people to stop, think about the case, and take the patient back, rather than ‑‑ if that patient had any particular features that were ‑‑

DR. FELDMAN: Mike, did you find that slide? Okay.

ACTING CHAIR LASKEY: Thank you.

Dr. Krucoff, do you have ‑‑

DR. KRUCOFF: Just a quick question about the communication pattern. I'm sure, being as it's you guys, you can understand one of the things we're going to try and do or wrestle with is to understand where all of these changing definitions or just issues seem to have arisen between what you know is coming in the FDA's view of the strong events, and ultimately have an understanding.

You had a couple of slides that were put up on data flow process, and several of you have commented on that. And I wonder, is anybody here from the external CRO? Or can anybody help me understand the background link of what data flowed from the external CRO to the sponsor, and ultimately, along the way, what the process was, then, for communicating as definitions were refined or evolved over the course of the trial in communicating back to FDA?

MR. WHITE: Hi. I'm Bill White, President and CEO of C2R. We were the external CRO involved with this trial. As the slide presents, what we were entailed with doing ‑‑ what we did for the M&M Committee was very simple. We collected all of the case report forms that came in from the centers, and then we went through a laborious process of accumulating the discharge summaries and the supporting documentation and hospital records.

We prepared case narratives for every case. That included a summary of the hospitalizations, all the case report forms, all of the documentation, and we prepared those in booklets for every meeting. The meetings were then scheduled on a routine basis with the committee, at which time we would send the books out from our office to the members of the committee.

We would send individual booklets to the primary and secondary reviewers, and they would make all booklets available to the committee for the meetings. During the meetings for the M&M Committees, we were always present, minutes were taken, all of the votes ‑‑ the material was reviewed, the adjudication process was documented, case report forms were filled out, all case report forms for the adjudication process were then signed by the Chairman, which is Dr. Carson.

At that point, all of the books were retained by us, and brought back to our office. At that point, what we did with the data was that data became part of the official database, in our clinical trial database, and that data was forwarded on a period basis with our monthly transmittals to the independent statistician, Dr. DeMets' group.

We did not forward any data at any time to the sponsor. The data always went from our office, from the M&M Committee case report form, to the independent statistician who did his analysis and then reported it to the Data and Safety Monitoring Board.

So that's what we did.

DR. KRUCOFF: Okay. So then, David, your data would go directly to the DSMB, one way?

DR. DeMETS: Yes. We prepared sort of an additional detailed monitoring report, which covered things from recruitment to primary safety, the whole double package, and we reported to the Monitoring Committee. At no time did we communicate anything about those reports to the sponsor. The only communication was with the Data Monitoring Committee, with the one exception that was noted when we had a discussion with the FDA about a different matter.

DR. KRUCOFF: That was the coronary sinus ‑‑

DR. DeMETS: Yes, that's right.

DR. KRUCOFF: Okay. And then, is it fair to say ‑‑ can somebody say the feedback from the line from DSMB to Steering Committee is simply the sort of go/no-go kind of communication, generic ‑‑

DR. DeMETS: Yes. The Chairman of the Steering Committee wrote a very perfunctory letter saying the committee met, reviewed the data, and recommended to continue.

DR. KRUCOFF: And then, the Steering Committee to the sponsor communications, can somebody characterize what those were likely to be?

DR. BRISTOW: Yes. The sponsor had a representative in an ex officio sense on Steering Committee calls. And whenever the Steering Committee ‑‑ in addition to that, whenever the Steering Committee thought there was an issue requiring sponsor input, we would communicate with them directly.

DR. FELDMAN: Does that ‑‑

DR. KRUCOFF: That was very helpful. Thanks. Maybe we can get ‑‑

ACTING CHAIR LASKEY: Yes, Dr. Yancy.

DR. YANCY: Just two questions. The first one is within the context of what Dr. Carson shared with us. Looking at slide 56, it's evident that the actual admit rates were higher than projected. And so for clarification purposes, since Dr. Saxon addressed the hospitalization question quite substantially, was the change in hospitalization more an operational change, so that it would be easier for them to track and follow as opposed to trying to enrich the event rate?

Because that has been a problem of a number of heart failure trials, and has necessitated a change in hospitalization. It looks as if this was more for the purposes of accurate data tracking. If you could just clarify that, if you would.

DR. CARSON: Yes. The change in the completing of the definition, if you will, for hospitalization, then, was related to trying to make verifiable data possible. We had thought that a 24-hour endpoint would be a reasonable one to use. And as I had said in my comments, during the previous trials that had used this endpoint ‑‑ maybe we could just go to backup slide 2.

This had been the endpoint that had been used. This was the way the ‑‑ the definition, really, for hospitalization has been an evolving one. You are very well aware that all-cause mortality had been the gold standard for trials for many years.

We didn't really see hospitalizations being adjudicated or included in primary endpoints, really, until the PRAISE trial in 1993. And that had a ‑‑ CV morbidity was a hospitalization for life-threatening CV cause, and it was for greater than 24 hours.

MERIT heart failure did all-cause mortality and all-cause hospitalization, and they started with a visit that was described in the protocol as being greater than 24 hours. But yet, if you look in their methods ‑‑ their methods paper, you find that the Endpoint Committee added a calendar date change if the dates ‑‑ if the times couldn't be verified.

VALHeFT had nothing in the primary protocol about time of hospitalization. The Endpoint Committee added on 24-hour duration, and then I chaired that committee and we realized that we weren't getting verifiable discharge times in many patients, particularly foreign sites. So we went to a calendar date change.

And then ‑‑ now, COMPANION fits in a little bit between VALHeFT and ‑‑ I have Overture on the bottom there. And we thought because we were at U.S. centers that we might be able to get admission and discharge times. The data, as you saw on the adjudication form, was in terms of calendar date change. When the committee looked within the records and tried to find the discharge times, we found that we couldn't always do that.

And we felt we were vulnerable, then, to a group coming back and saying to us, "Well, could you really verify that these were 24-hour times? Could you really get the discharge times?" We would have had to say we couldn't always get those.

So we felt that a 24-hour date change was not something that was verifiable enough for this endpoint, and we felt that a calendar date change, which had then been evolving into being really the standard for clinical trials, was what we should use. That was after a small number of events had been done, so it was entirely for date clarity.

DR. DeMETS: Just a further comment. We didn't convey any sense of event rates to anybody. It would have been difficult for them to keep score. They perhaps could have with a ‑‑ but they ‑‑ it wasn't something they were aware of the dates, so they didn't know anything about event rates at that point in time.

DR. BRISTOW: Well, I will underscore that. We have been under the assumption that it was going to take 2,200 patients to achieve this 1,000 target events. And, in fact, when we were called in to the DSMB in November 2002 and said that you've got your target number of events, we were, frankly, shocked that the event rate was that high. We had no sense that the event rate was that high on the Steering Committee.

DR. YANCY: One other question, Dr. Carson. Given the threshold that you set for the calendar date change, do you have any feel for the number and the kind of clinical experiences that didn't met that threshold? Were these just parenteral diuretics for a slight change in symptoms? Was it a large number? Small number? Do you have any feel for those that didn't reach that threshold?

DR. CARSON: We would ‑‑ because the data that was collected was in terms of a calendar date change from the sites, we would not have had events that then we would have excluded.

I do have to say that, as I have thought about this in multiple clinical trials, I would have to say that these events would have to be exceedingly rare in which a patient would be admitted to the hospital, not treated in an outpatient setting, but admitted to the hospital, and then discharged sometime late at night after therapy.

It's not a practice I am familiar with as a practicing clinical cardiologist for close to 20 years. And I think within the clinical trial milieu you have to be exceedingly rare. This has been of concern previously. This was brought up when VALHeFT presented its data in 2001, and at the time we did not have data then either. No clinical trial has really presented ‑‑ has really collected data that I know of on these kind of events.

The VALHeFT question before the panel in 2001 did bring up the issue, and the Overture trial, for example, went back and looked at their heart failure hospitalizations and found a very small number of them that were, in fact, less than a 24-hour period or did not involve a calendar date change. So I'm afraid I don't have any data beyond that.

DR. YANCY: No, that's helpful. It seems as if it was, then, largely operational. I just have one short question for Dr. Saxon. It has to do with the safety issue. The chart that is slide 99 shows that the coronary venous trauma occurred in 3.7 percent of cases. And it appeared to be of no really meaningful consequence.

I'd just like to understand if those were episodes of tamponade that were just monitored or if these really were inconsequential with just extravasation of dying. Can you just help us understand that? At first glance, it seems like it would be a fairly traumatic event. But it seems as if the consequences were less so.

DR. SAXON: Great. I'm happy to answer that. Let me just reflect back to your question to Dr. Carson, which was what was sort of types of things that occurred in this trial that might ‑‑ that occurred in this trial that might not meet the calendar date change.

And one thing we could look at would be, for instance, lead revisions for any reason. Thirty-six of the 50 lead revisions did trigger a calendar date change, so a minority didn't, just to give you a sense of those types of events.

Related to coronary sinus trauma, you're right, the majority of coronary sinus venous traumas, which were carefully classified in this trial as either dissections, meaning that there was simply dye in the lumen of the vessel, a perforation indicating that the dye was free-flowing beyond the vessel but did not require an intervention, required observation alone, and in some instances one even proceeded with the implant, who had tamponade would be defined as requiring an intervention or resulting in some type of event.

So when you look at coronary venous trauma, the majority of those events were staining or required a non-invasive or just an observation period for resolution. But some of them ‑‑ some of the perforations as well as obviously the tamponades did require some type of invasive procedure to correct.

DR. YANCY: Thank you.

ACTING CHAIR LASKEY: Dr. Somberg, and then we'll take a break.

DR. SOMBERG: Dr. Bristow, you were discussing the issue of the availability of devices in the course of the trial, and that this was considered a problem because people might want to take their patient out of the study and give them the benefit of something that was approved.

For that reason, it was introduced ‑‑ if I'm paraphrasing you correctly, it was introduced ‑‑ the concept that to do that there would have to be a worsening of congestive heart failure, and that would have to be an indexed hospitalization.

With that said, wouldn't that then be sort of an admonition or a call to increase the number of hospitalizations in the CRT-P group? And if that be the case, or possibly the case, can you show me a data breakdown of the number of hospitalizations in CRT-P before that edict was announced and after it?

DR. BRISTOW: Well, I can't pinpoint the data. All I can say is that the primary event rate was linearly consistent over time. That is, there was no inflection of the primary event driven by hospitalizations ‑‑ 90 percent of the primary events hospitalizations. There was no change in the primary event rate over time in the OPT group, and ‑‑

DR. SOMBERG: Am I right to assume that was sort of like a midpoint decision in the trial? Because looking at that peak of entry, and then a decline rapidly ‑‑

DR. BRISTOW: Yes. So that obviously ‑‑ that decision had to be made after these devices were available. So it's ‑‑ you saw the enrollment per month, a bell-shaped curve, and it was beyond the peak of that bell-shaped curve and we began to institute these measures. And it did not lead to an increase in the number of primary endpoints.

And I can tell you that, you know, we often rejected the data as not being adequate. They had to provide an admission note if the patient was in the hospital, clearly showing that there was progression of heart failure. They had to provide data on the treatment of heart failure, which had to be substantive. That is, it had to be IV therapy such as IV Lasix, for example. Backup slide 19.

So this was a very stringent process. The Steering Committee was aware that this had the potential to, as you paraphrase your thoughts, create endpoints. But I don't believe this actually did based on the stringency of the process.

And I will also say that the investigators were strongly encouraged to maintain their equipoise. So here are cumulative ‑‑ this is cumulative by month. So that's not ‑‑ there's another ‑‑ yes, you don't see a turn up anywhere. Log log plot would be good. There's no spike, there's no up-tick in that curve, and there are better curves to look at perhaps.

But what I was saying ‑‑ okay. Now, that last little point is out there where there's maybe one patient left in the OPT group out there at the end. So that needs to be ignored. But ‑‑

DR. SOMBERG: Doesn't this need to be at a flexion point of 5.5?

DR. BRISTOW: So there wasn't any change in event rate over time. And, again, the investigators really did a great job of maintaining their equipoise. Our message to them was, we haven't proven this therapy works in this kind of advanced heart failure population.

And the data that you're seeing or that led to the approval of these devices were based on much less sick patients. These were not hard endpoints. This wasn't true intention to treat from the start of randomization ‑‑ none of these data. And I would say that 95 percent of the investigators truly believe that and maintain their equipoise.

All right. Here we go. This is the best slide for this purpose. This is the actual rate by month, and you can see the OPT group is not up-ticking anywhere.

ACTING CHAIR LASKEY: Well, it's a notable finding, because this panel has seen expansions in use of devices shortly following the approval. So this would be certainly unique and an exception. But ‑‑ do you have one more question?

DR. SOMBERG: Yes, I have one more. The other thing was it was mentioned the duration of hospitalizations might be different between the initial implant and the CHF therapy. I wonder if you have the data in terms of duration of hospitalization for the CRT-D versus the CRT ‑‑

DR. BRISTOW: Yes. We showed earlier ‑‑ data we have to show you we had on earlier.

DR. FELDMAN: Here it is.

DR. BRISTOW: Here is what we have. And so this is implant hospitalizations, elective implant hospitalizations, in either group, drop-ins in the case of OPT, and then CRT-D upfront or reimplant attempts versus medical hospitalization that were part of the primary endpoint.

DR. SOMBERG: Yes. But I'm asking to see the total hospitalizations of the two groups in terms of duration.

DR. BRISTOW: Okay. We have ‑‑ that would be in the morbidity data we showed. So just give us a second; we'll pull that up.

Again, as has been alluded to a couple of times, looking at hospitalization data in isolation in a trial where there's a competing risk of death of problematic. And so we always start with a disclaimer. But if you go to the right, this cardiac morbidity is in hospitalized patients is how it was done. So it's the duration of ‑‑ it's not purely hospitalization. It's the duration of the event driven by hospitalization.

And, obviously, there seems to be a difference in favor of CRT-D. It's not exactly what you're looking for, but it's driven by what you're looking for.

ACTING CHAIR LASKEY: Great. Thank you.

I have 11:15. Let's regroup at 11:30 and have the FDA presentation.

Thank you very much.

(Whereupon, the proceedings in the foregoing matter went off the record at 11:18 a.m. and went back on the record at 11:34 a.m.)

ACTING CHAIR LASKEY: We're doing well, folks, if we can take our seats and resume. Thank you. I promise that everyone gets where they need to be this afternoon, so let's move forward.

DR. FARIS: Ready to get started.

ACTING CHAIR LASKEY: Thank you, sir.

DR. FARIS: Good morning. My name is Owen Faris and I'm FDA's lead reviewer for this submission in which the sponsor is seeking expanded indications and claims for their CRT-D devices. The physical reviewer for this submission was Dr. Barbara Krasnicka. The clinical reviewers were Dr. Scott Proestel and Dr. Ileana Pina and bioresearch monitoring was directed by Rachel Solomon. The regulatory background for the COMPANION clinical trial is extensive and includes the following important events.

The COMPANION was approved under a binding agreement between the sponsor and FDA formalized September 8th, 1999. On January 20th, 2000 the first patient was enrolled. On May 2nd, 2002, the sponsors CONTAK CD device received FDA approval. On November 30th, 2002, the COMPANION trial was stopped for reasons previously discussed by the sponsor. On January 26th, 2004, the sponsor's CONTAK TR, Renewal TR devices received FDA approval. Thus, at that point, both devices which had been studied in the COMPANION trial were market approved.

On March 26th, 2004, the submission currently under review was received by FDA. The formal agreements between FDA and the sponsor regarding the COMPANION clinical trial included agreement on the inclusion and exclusion criteria, the primary and secondary hypothesis and the statistical analysis plan. It was agreed that the statistical plan would not support CRT-D versus CRT-P comparison. In addition, to address the issue of multiplicity, the statistical plan required consistency across the primary and secondary end points in order to evaluate the results from any one end point.

The sponsor's proposed indication requests the following changes based upon results from the COMPANION clinical trial; an expanded indication to include the entire population described in COMPANION and new claims based on the primary composite end point as well as the secondary end point of mortality.

The proposed indication reads as follows; Guidant Cardiac Resynchronization Therapy Defibrillators are indicated for patients with moderate to severe heart failure, NYHA III/IV, and remain symptomatic despite stabile optimal heart failure drug therapy and have left ventricular dysfunction, EF less than or equal to 35 percent and QRS duration greater than or equal to 120 milliseconds. Guidant Cardiac Resynchronization Therapy Defibrillators have demonstrated the following outcomes in the indicated patient population specified above. Reduction in risk of "all-cause" mortality or first "all-cause" hospitalization, note hospitalization is defined as administration of IV inotropes or vasoactive drugs greater than four hours outpatient or inpatient or admission to the hospital that includes or extends beyond a counter date change, reduction in risk of "all-cause" mortality, reduction of heart failure symptoms.

FDA's review covered the following areas; COMPANION primary and secondary end point results, COMPANION hospitalizations and adverse events, consistency with a pre-specified clinical and statistical plans and presentation of data and device labeling. At this time, I would like to introduce Dr. Barbara Krasnicka to present FDA's statistical review.

DR. KRASNICKA: In my presentation, I will focus in on the problems connected with the study design, data quality and study scholar analysis. As it was mentioned before, the objective of this study was to demonstrate the safety and effectiveness of the OPT plus CRT-D and OPT plus CRT-P through the comparison with OPT alone. In this statistical review, only a comparison of CRT-D versus OPT will be presented. As mentioned before, the COMPANION trial was a prospective multi-center randomized study on patients suffering heart failure.

The clinical trial for all the group, sequential design. The study was planned to stop after 1,000 primary end point events would be identified. It was expected that compared to the OPT alone, the CRT-D could reduce combine "all-cause" mortality and "all-cause" hospitalization which was the primary effectiveness end point. And "all-cause" mortality and cardiac morbidity which were the secondary effectiveness end points. The safety end point was not specified.

Quality of data is influenced by clear definitions of response variables and methods used towards data collection, editing and assessment. The primary effectiveness end point was modified three times during the study. The end point was originally defined as "all-cause" mortality and "all-cause" hospitalization where "all-cause" hospitalization was defined as admission to a hospital for any reason. In addition, this end point would include emergency room visits that resulted in IV therapy. "All cause" hospitalization definition was finally revised as the one for which the discharge date was different from the admission date or as hospitalization longer than four hours during which patients received IV therapy.

The collection of hospitalization events was based only on admission and discharge dates, not taking into account exact time. Therefore, the capture of hospitalization event longer than four hours during which patients receive IV therapy, was based on the duration of the IV therapy as recorded in the follow-up case report form.

However, some hospitalization events did not have a case report form. Therefore, there are some concerns that such events may not be captured. The study stopped in December 2002. Some patients were followed up only for a few weeks or days. At the moment of trial stopping 941 primary end point events had been submitted. This means the target number of primary events had been approximately reached. However, there were many withdrawals from the study. The withdrawal rate was especially high in the OPT group. At 12 months, it was 21 percent in the OPT group but only four percent in the CRT-D group.

FDA is concerned that worsening of patients health status was probably the reason for many withdrawals. Due to many withdrawals and an imbalance between the two treatment groups in the number of withdrawn patients, the withdrawn patients were asked to consent again to collect end points data and status. FDA is concerned that post-withdrawal information regarding hospitalization may be unreliable.

The differences between groups with respect to the primary effectiveness end point and all "all-cause" mortality work is low grant statistics. Kaplan-Meier method was applied to estimate the survivor functions for the two groups and the Cox Model was used to estimate hazard ratio. In the case of cardiac morbidity and adverse events, mainly the exploratory analysis were performed.

Now, let us discuss the statistical analysis of the primary effectiveness end point. This means analysis related to combine "all-cause" mortality and "all-cause" hospitalization. The data set contained 202 and 386 primary events in the OPT and CRT-D arms respectively. It is worth noting that the primary end point was driven mainly by hospitalization events which constitute over 92 percent of all primary end points.

This slide shows the class of estimates of event free functions based on the Kaplan-Meier method. The figure demonstrates some separation of both curves over time but the curves are clearly separated only in a period of time, about one year after randomization. After 800 days, the estimations are based on the relatively small number of observations and may be unreliable.

To perform meaningful survivor analysis, for example, to apply the Kaplan-Meier method, some assumption should be made, among other assumptions are quality of data set was good, the primary effectiveness and definition was not changed, and censoring was non-informative. Censoring is non-informative if it is independent of the occurrence of an event. This means patients' withdrawals should be at random and should not be caused by deterioration n the health condition of a patient. It is essential to notice that the fundamental for the survival analysis assumption of non-informative censoring may not be satisfied for this study. The even free time of some patients was censored due to worsening of their health status.

Therefore, the censoring may be informative. This means it may not be independent of the occurrence of an event. Now, let us assume that the before mentioned assumptions are valid and we can take a closer look at the event rate changes. Changes over time of the event rate are given in this table. The smallest differences, one to two percent, is an event rate between the two groups occur during the first several days and around 200 days after randomization, and the largest difference, 10 percent, took place about 400 days.

Under our temporary assumptions the results of statistical analysis are as follows. Survivor functions for the CRT-D and OPT groups are different at significant level 0.025 based on the Wilcoxin test which is more appropriate than log rank test in this situation. The Cox proportional hazard model supplies the hazard ratio equal 0.81, at significant level 0.015. It is worth noting that hazard functions clause and Schoenfeld residuals may not support proportionality assumption which is essential for the Cox model.

Therefore, the claim that CRT-D therapy reduces the relative risk about 20 percent is questionable. The results of the statistical analysis for the primary effectiveness end point may be problematic because the primary effectiveness end point definition was changed during the study. The assumptions on the line statistical models use may not be satisfied. The censoring mechanics applied may not be independent on the occurrence of the end point. The censoring was probably informative.

The hazard functions and the Schoenfeld residuals suggest that the proportionality assumption which is essential for the Cox model, may not be valid in this case. Statistical analysis for "all-cause" mortality secondary end point raises similar statistical concerns as the primary effectiveness end point analysis and will be discussed here shortly. Let us now assume that the censoring is non-informative. We can use the Kaplan-Meier method to estimate the survival function for the two groups. The effect of CRT-D therapy on the "all-cause" mortality is presented in this figure. The plus show that the estimated survival functions are different and the survivor function for the CRT-D group is almost always greater than or equal to the one for the OPT group.

Please pay attention to the scale on the vertical axis. In this figure, the scale is the same as in the figures for the primary effectiveness end point. In the next figure, the scale on the vertical axis was changed and confidence intervals for the Kaplan-Meier survival functions were added. The black curves are the survival functions shown in the previous slide. The red lines are the upper and lower confidence limits of the survivor functions for the OPT group, while the blue ones are for the CRT-D group. The confidence intervals for the survivor functions are crossing each other and even crossing the CRT-D survivor function itself.

Changes of the death rate over time by treatment groups are shown in this table. During the first 150 days after randomization, the differences in death rates between the two groups are small, maximum two percent, however, at 400 days, death rates for the CRT-D and OPT groups were 12 and 22 percent respectively, so therefore there is a difference in the survivor at 400 days is about nine percent in favor of the CRT-D group.

In the case of "all-cause" mortality and the tentative assumptions, survivor functions for the CRT-D and OPT groups are different at significant level 0.003. The Cox model supplied the hazard ratio 0.64 at significant level 0.003. But for the "all-cause" mortality, again, the statistical results may be problematic because the assumptions underlying the statistical methods used may not be satisfied. Hazard functions and the Schoenfeld residuals do not reasonably support the proportionality assumptions that is essential for the Cox model.

Now let us discuss the cardiac morbidity. Sponsor considered only cardiac morbidity events which occurred in hospitals but some events could and did take place outside hospitals. The hospital cardiac deaths is only a part of the cardiac morbidity. There were five cardiac deaths in the CRT-D group and three cardiac deaths in the OPT group during the first 30 days after randomization; whereas, numbers of only hospital deaths was zero and two respectively. This is shown in this table. Therefore, cardiac morbidity based only on hospitalization data that was used by the sponsor does not supply the full information on all cardiac morbidity events.

Adverse events were defined by the sponsor as undesirable clinical outcomes and included device related events as well as events related to the patient's general condition. This table presents the over times summary of all adverse events through six months. We can observe that over time the number of events increases rapidly. During additional 120 days, the numbers are double in the two groups. Assuming that each was to follow up patient before the six months was free, the adverse event rates were 3.21 and 2.05 for CRT-D and OPT groups respectively.

Using the worst case scenario, the adverse event rate through six months was 3.73 for the CRT-D arm while the similar rate for the OPT group was 2.80. According to both, the worst case and best scenario analysis, the OPT patients experienced fewer adverse events during six months after randomization. It is worth noting that the validity of sponsor statistical analysis is of concern since correlation between multi-events within a patient was ignored. Time of an adverse event occurrence was not taken into account. Many follow-up patients were excluded. Therefore, all exploratory analysis should be interpreted with caution.

The statistical review conclusions are as follows: treatment comparisons for the primary effectiveness and mortality end points should be interpreted with caution because of changes of "all-cause" hospitalization definitions, withdrawals not clearly independent of outcome, and open label and design. All cardiac morbidity events that occurred outside hospitals were not taken into account. Lost follow-up patients, correlation within a patient and times of the events occurrence were not included in the sponsor's statistical analysis of cardiac morbidity and averse events. Thank you for your attention. Now, Dr. Proestel will present clinical review of the study.

DR. PROESTEL: Hello, thank you. I am Scott Proestel. I'm the Medical Officer at the US Food and Drug Administration. For my presentation, I will very briefly summarize COMPANION design, issues surrounding the primary end point and secondary end points, some additional FDA efficacy analysis that were performed as well as a safety analysis.

We've already reviewed the COMPANION trial quite well, I believe, so I will skip through a number of slides. And I think you're familiar with this as well. This describes the primary and secondary end points. As you know, the primary end point was timed to "all-cause" mortality plus "all-cause" hospitalization. The secondary end points for the trial are listed as well. The results have been quite well reviewed as well. Just briefly 1638 patients were enrolled, 93 percent were randomized. Enrollment occurred between January 2000 and November 2002.

As you can see on the slide, those are the numbers of patients that were ultimately enrolled in each cohort. Here are the baseline characteristics for the three cohorts. In particular, I'd certainly like to focus on the CRT-D and the OPT cohorts. Two things that I would like to mention is that within the cohorts, there was a modestly higher proportion of Class IV and ischemic patients in the OPT arm. Mortality in Class IV patients was 2.9 times higher than in Class III patients and 1.7 times higher in ischemic patients than in non-ischemic. Therefore, both of these imbalances favor the device arm.

This slide provides additional baseline characteristics which appear to be well-matched. One thing I'd like to say as well is that my presentation will provide only descriptive statistics and should be considered adjunctive to the statistical findings discussed by Dr. Krasnicka. All events from randomization until patient withdrawal or November 30th, 2002 are included. This is the primary end point that was specified in the protocol which I believe you're all familiar at this point.

However, the definition changed three times during the trial. The definition initially was changed in March 2001 to include only hospitalizations lasting greater than 24 hours. This definition changed again in February 2002 to include only hospitalizations for which the discharge date deferred from the admission date. Regarding the infusion requirement, there was no required duration specified in the protocol, although a duration of greater than four hours was ultimately used in the analysis.

As the sponsor has provided case report forms from the beginning of the trial that also specified this greater than four-hour time requirement, it appears that this last change to the definition did not occur during the trial. A compelling explanation for the change in definition would have been that the new definition is inherent to the old; meaning that to be hospitalized necessarily means staying in the hospital overnight. However, this is not the case.

First, if this were true, the revisions would not have been necessary. Second, the trial temporarily used a different definition, meaning requiring that a hospitalization be greater than 24 hours in duration. Finally, I have only a decade of experience in clinical medicine, but during that time I have hospitalized patients for less than 24 hours and for less than an overnight stay so can state with certainty that neither requirement is inherent to being hospitalized. So far from adding clarity, the requirement of a minimum duration makes the definition more complicated. After all, to establish the duration of hospitalization, one needs an admission order and a discharge order. However, to abide by the pre-specified definition of the primary end point, one only needs the admission order.

If the intent was to require a hospitalization of a certain duration, one would argue that it should have been stated up front. So what was the ultimate definition of the primary end point? While this is a busy slide that is somewhat the point, the definition was considerably more narrow than the encompassing claim of "all-cause" mortality plus "all-cause" hospitalization. So as can be seen, the hospitalization had to be associated with a date change, could not be a hospitalization associated with an implant or a repeat attempt at implant and could not be considered elective and associated with the device. In addition, events that were not hospitalizations were considered as such for the purpose of the primary end point.

Getting back to the issue of the changes that occurred to the primary end point, the first question one could ask is whether the new primary end point is clinically important. I think that the answer is, is yes and in fact, it is likely more important than the original version due to the requirement for a longer hospitalization. However, the next question that must be asked is, do the changes that occurred in the primary end point undermine our belief in the observed effect?

This is a concern for FDA because if the primary end point is modified in response to events occurring during the trial, this would allow for the possibility of modifying the end point in such as way as to favor the device arm. This is one of the issues that FDA will ask the panel to address.

This slide presents data related to "all-cause" mortality which was a secondary end point. In addition, all cardiac death and the sub-groups of pump failure deaths and sudden cardiac death are provided. This table presents all deaths during the trial, including those that may have occurred following subject withdrawal if that data was available and is presented in terms of death per 100 patient years of follow-up. The CRT-D arm is associated with a reduction not only in sudden cardiac death and pump failure death but in cardiac death overall and "all-cause" mortality. There has been some concern in the public that the CRT aspect of the device, of the CRT-D device, might be associated with an increase in sudden cardiac death. However, as can be seen here, the improvement in pump failure death overwhelms the modest increase in sudden cardiac death leading to an improvement in cardiac death and "all-cause" mortality associated with the CRT intervention.

So solely for the purposes of understanding the CRT aspect of the CRT-D device, these point estimates might be considered reassuring. Cardiac morbidity was another secondary end point. It was defined as the occurrence of the following events listed on this slide and I believe this has been addressed before, so I won't read them to you. These events were also considered cardiac morbid events.

However, the definition that was used did not match the definition provided in the protocol. The definition that was used for cardiac morbidity was any hospitalization during which one of these specified cardiac morbid events occurred. Therefore, a single hospitalization that had multiple cardiac morbid events would only count once towards the end point. Using this definition, as you can see, there was a mean of 0.5 events per year in the CRT-D arm and 1.0 events per year on the OPT arm. The FDA does not have the data to calculate the original cardiac morbid end point as specified in the protocol.

I would like now to discuss some additional analysis that were performed for the purposes of device labeling which may help to clarify the results of the study. These were not specified end points for the trial. This may, in some way, address a concern that Dr. Brinker had discussed. As the primary end point only counted the time to first event, any subsequent hospitalizations were not counted. Therefore, FDA felt it would be informative to perform an additional calculation, the "all-cause" hospitalization rate which was not specified in the protocol. In this evaluation of hospitalizations for any cause, which included implant attempt hospitalization, there was a mean of two hospitalizations per year in the CRT-D arm and 1.6 hospitalizations per year in the OPT arm.

In addition, the CRT-D patients were in the hospital for a mean of 11 days during the year and in the OPT arm 10.7 days per year. There have been arguments made as to why it might not be reasonable or appropriate to include the implant attempt hospitalizations in an "all-cause" hospitalization analysis which I would like to now address.

It has been argued that the implant hospitalization is a single non-recurring event. It is not. Forty-nine of the patients had to undergo two implant hospitalizations and two patients underwent three. And in approximately four to six years the device subjects would need to be hospitalized again to have the device replaced due to battery depletion. Even if one believes that the implant hospitalizations were recurring but at a trivial rate, the rate was certainly greater than that for say cholecystectomy which was included as a hospitalization during the study and luckily occurs no more than once in a lifetime.

The fact of the matter is that each of the causes of hospitalization is occurring at a given rate and the implant attempt hospitalization is not even the one associated with the lowest rate, so why exclude it. It has also been argued that the -- including the implant attempt does not characterize the effect of the device. This is true and this is the point. The encompassing claim of "all-cause" hospitalization by its very nature includes events that may not be tightly linked or linked at all to the action of the device. Indeed elective hospitalizations were included as events that counted towards the primary end point, so once again, why exclude implant attempts?

Finally, even if one decides to ignore implant hospitalizations, it may be worth noting that the effect of the device on hospitalization was not of sufficient magnitude during the trial to account for the implant hospitalizations that were required to get the device. I would like to emphasize that FDA is not advocating a change in the primary end point. We are merely attempting to make the case that this additional analysis of "all-cause" hospitalization is reasonable, clinically relevant and may aid patients and physicians in their understanding of what may be expected with this device therapy.

This slide provides the FDA analysis of the implant hospitalizations which was considered important to characterize despite not being an end point of the trial. As can be seen, 541 patients had a successful implant, 47 has unsuccessful implant and seven were randomized to CRT-D but never underwent a procedure. The mean duration of hospitalization was 2.9 days.

With respect to safety, FDA reviewed all adverse events during the trial. These were defined as undesirable clinical outcomes, including device related events as well as events related to a patient's general condition. The first set of numbers provides the total number of adverse events, not adjusting for the larger number of subjects in the CRT-D arm and the moderately longer follow-up in that arm. The rates adjust for these issues and you can see that the device arm had a greater rate of adverse events. However, the adverse events in the device arm were not of a rate or severity beyond that which might be expected for the intervention.

Indeed, as can be seen in this slide, the proportion of adverse events that were complications was actually lower in the device arm. An observation was defined as a clinical adverse event that was correctable by non-invasive measures and a complication defined as a clinical adverse even which required invasive measures to correct. Therefore, complications on average are more likely to be significant adverse events. And it is reassuring that the proportion of adverse events that were complications was, in fact, lower in the CRT-D cohort.

What I would like to do now is let Dr. Owen Faris present conclusions for the FDA presentation. Thank you.

DR. FARIS: In summary, FDA's review covered the following areas; COMPANION primary and secondary implant results, COMPANION hospitalizations and adverse events, consistency with pre-specified clinical and statistical plans and presentation of the data on device labeling. With regards to the primary end point, modifications were made to the hospitalization definition, part of the primary end point, during the course of the COMPANION trial. Fundamental statistical assumptions underlying some analyses may not have been met. Where the COMPANION demonstrated a benefit, the primary end point as originally defined is unknown. FDA requests guidance from the panel in interpreting the modified primary end point.

With regards to the secondary end point of mortality, the CRT-D device was associated with a decrease in "all-cause" mortality compared to OPT. However, fundamental statistical assumptions underlying parts of the analysis may not have been met. Since the pre-specified statistical plan required consistency between the primary and secondary end points, FDA requests guidance from the panel in assessing the impact of modifications to the primary end point on interpretation of the mortality benefit.

With regards to additional concerns raised by FDA's review, the sponsor's analyses included data obtained from patients after withdrawal. When implant hospitalizations were included, the CRT-D device was associated with an increase in "all-cause" hospitalizations compared to OPT. The CRT-D device was associated with an increase in adverse events compared to OPT. FDA requests guidance from the panel in determining how these considerations should impact the sponsor's CRT-D labeling.

Thank you very much.

ACTING CHAIR LASKEY: Thank you. Panel members? Dr. Normand.

DR. NORMAND: I just want to beat a dead horse again, but I need to get some clarification on the definition of "all-cause" mortality. So just to state it in my understanding of what's been presented, it is my understanding that the initial protocol stated "all-cause" mortality and didn't -- I guess didn't give a time frame for it. Is that correct?

DR. PROESTEL: The definition for death remained constant throughout the trial.

DR. NORMAND: Okay, but it was just -- it said, I'm sorry, "all-cause" hospitalization was just "all-cause" hospitalization. There was no timeframe of the "all-cause" hospitalization.

DR. PROESTEL: Not in the protocol.

DR. NORMAND: Not in the protocol. So that -- no one pushed for a definition. One just said, okay, "all-cause" hospitalization.

DR. PROESTEL: With the caveats of the greater than four hours of IV infusion and that the implant attempt would not be counted. Beyond that, it was "all-cause" hospitalization including elective hospitalizations.

DR. NORMAND: Okay, and another point of clarification. It's indicated that the definition changed three times. Hospitalizations greater than 24 hours and then the next one was a hospital in which a calendar date it was apparent. It seems to me for the first to be true, the second has to be true. Anything greater than 24 hours by definition the calendar date has to change.

DR. PROESTEL: Right, correct.

DR. NORMAND: So if my understanding is correct and I may be wrong about this, if you're going with the greater than 24 hours, then indeed, using the second definition, hospitalizations for which there was a calendar date change, you could actually include patients that were hospitalized for less than 24 hours, correct?

DR. PROESTEL: Correct.

DR. NORMAND: Okay, and then my last just clarification, help me think through some things. It is, I think you indicated that there was -- there were revisions but I heard a little bit earlier that there was never a revision of the data collection form. Did you mean revisions to the numbers that reported to FDA or did you mean revisions to the data collection instrument?

DR. PROESTEL: Revisions to the primary end point, I mean, you can collect data on a case report form that is not necessarily -- in fact, most of the data on the case report form is not related to the primary end point. So the fact that that data is on the case report form, certainly does not mean that the primary end point was, in fact, a date change or 24 hours. It should have been what was stated in the protocol.

DR. NORMAND: Thank you very much.

ACTING CHAIR LASKEY: All right, next? Yeah.

DR. KRUCOFF: Dr. Krasnicka, I'm going to ask you for help because -- and I want to talk just about mortality, okay, death. Your contention that I'm just going to need some education on, I guess, about the underlying assumptions for the Cox model.

DR. KRASNICKA: Yes.

DR. KRUCOFF: Does that effect the mortality reports and effect of the device on mortality in this model?

DR. KRASNICKA: Yes. This means -- the second part, the sponsor plan is that there is 66 percent of reduction in related risk if the assumption is not -- we don't know exactly, again, because it's really this estimation is biased.

DR. KRUCOFF: So to the relative lay person, can you help me understand what's bad about this?

DR. KRASNICKA: I can show you Schoenfeld residuals and you can see how this estimation is change over time. It's from the plus to minus and this is mortality -- slide. The next one. And you can --

DR. KRUCOFF: Would you mind getting closer to the mike, I can barely hear you.

DR. KRASNICKA: You can see that the coefficients at treatment in Cox model is changing from the plus to minus and then to plus. This means that the proportionality assumption is not true of the Cox model and we cannot claim, for example, that there is 66 percent of the reduction in related risk.

DR. NORMAND: Perhaps if I could -- if I could maybe just ask a question to perhaps clarify the answer. I guess part of the panel members are wondering if the Cox -- if you use a Cox model to analyze the data, and you reported an estimate based on a Cox model in which the proportionality assumption is violated, I think that's what you're suggesting.

DR. KRASNICKA: Yes.

DR. NORMAND: The Cox model, that the proportionality assumption was violated, in which case it says that they cross and you wouldn't want to say that it, indeed, was a -- you know, one way or the other. They crossed and so sometimes it's good and sometimes it's bad. Is that a fair characterization of what you're --

DR. KRASNICKA: Yes, yes.

DR. KRUCOFF: Okay, so to my mind, when I look at this, what I see is that, in fact, the relative benefit to death rate over time in a population treated and not treated with the device, may be different at different times --

DR. KRASNICKA: Yes, yes.

DR. KRUCOFF: -- along the time.

DR. KRASNICKA: Yes.

DR. KRUCOFF: It's not uniformally beneficial.

DR. KRASNICKA: Yes.

DR. KRUCOFF: But how much impact does that then have on the end conclusion or inability to reach a conclusion that at the end of 300 days or a fixed time period that ultimately in a population who has some heterogeneity through a range of mechanisms that may behave differently at different times, that at the end of a prolonged observation, you could make a wrong claim.

DR. KRASNICKA: The best way it would be adjusted for the baseline providers and to check if, for example, the models are correct, are good for this case, and to check for example, how centers have impact on the result because in the case of the survival analysis, really you have to adjust for the covariance to get not bias estimation of the treatment. It's completely different. For example, in the case of binary outcome, at one year, you don't need, really to adjust for the covariance. That --

DR. KRUCOFF: So has anybody done that? Have you guys done that? Can anybody show us any adjustments?

DR. KRASNICKA: No, I got that set only for really two, three weeks and I didn't have time.

DR. KRUCOFF: All right, one other clarification question and I'm done. We've obviously heard clearly that there's a concern about whether the censoring process was informative.

DR. KRASNICKA: Yes.

DR. KRUCOFF: But as I understand it, at least, if it is, if basically patients who in the OPT arm, were getting sicker so they got pulled so they could not be a violation, go and get their device through other means, if the presumption is those patients were getting sicker and they are withdrawn, doesn't that -- isn't that actually unfavorable for the device?

DR. KRASNICKA: Yes, but when you look at the "all-cause" hospitalization definition, definition was changed and really all hospitalization for any reason was dropped and when I was thinking that maybe the patients from the CRT-D group got problem with device, and for example, went to hospital for one, two hours, so we don't know really, what's happened with the primary effectiveness end point.

DR. KRUCOFF: Okay, I understand the definition got changed, but I think this is going to be really important. To me, are you saying that there's some relationship in your mind? Are you guys thinking that the change in the definition of "all-cause" hospitalization somehow relates to an informed or biased censoring or withdrawal of patients from the OPT group? Or are these separate issues?

DR. KRASNICKA: Separate issue.

DR. KRUCOFF: They're separate issues. So all I was asking is, on the informed -- on the concern about informative censor. That's all I was asking --

DR. KRASNICKA: Yes, okay.

DR. KRUCOFF: -- is if I understand the concern, which is a real concern, at least the way I see that one issue, it's actually unfavorable to the device if patients who are getting sick are in the control -- the in OPT arm, are getting dropped out --

DR. KRASNICKA: Yes.

DR. KRUCOFF: -- that would be unfavorable for the device. Is that not true --

DR. KRASNICKA: Yes, could be.

DR. KRUCOFF: -- in terms of claiming a benefit for the device?

DR. NORMAND: I think you could make arguments along a number of different directions on that. I just feel I have to say this.

DR. KRUCOFF: I'm just asking a question.

DR. NORMAND: No, and I'll give you at least my opinion on that. And that is if -- certainly one could argue that they could be healthier, there's no doubt about that, but one sicker -- but only may say they're healthy enough to receive the device, so there is some selection. So you could in some ways argue about them, yes, maybe they were sick enough to get the device, but yet, they had to be healthy enough to actually receive the device in the absence of this. So there is a selection process in there that does raise a concern -- not raise a concern but --

DR. KRUCOFF: But assignment to the device was randomized.

DR. NORMAND: Well, no, you're saying there are a group of people -- I'm asking a hypothetical question, so there's a hypothetical question where someone was randomized to treatment one or treatment two. I'm saying it hypothetically because I don't want to -- I don't know the answer to this in this particular situation but if they were randomized to treatment one or treatment two and another therapy becomes available and someone says, "Gee, I want to get it, I want to pull out of this and get this", there are considerations that say, "Yeah, I recommend you actually do that".

And, yes, they may be sick enough to need the new device but often there are patients that get devices that are healthier, because they're robust enough to actually get the device rather than the physician saying, "No, stay on the current treatment". So you could argue both ways.

DR. SOMBERG: But the trouble with that is it sort of addresses the question that Dr. Proestel showed me that there was really no major inflection point in the -- in the data because that would occurred during the course of the trial when these devices became available and there wasn't a change in the number of patients who were in the pharmacologic therapy were then being censored from the study. Am I correct in that?

DR. NORMAND: I'm not sure about the answer to that question but I am sure about the answer to the question that it's not necessarily true that it would have favored the therapy arm if some people left. I can't conjecture on why there wasn't because normally you see a big jump.

DR. KRUCOFF: I'm sorry, I lied. I have one other quick clarification, Scott, at least because it's on the record. In your slide, showing the baseline characteristics, I just want to make sure that I heard what you said versus what I see. The Class III, Class IV ischemic population, Class IV population slightly higher incidents in the CRT-D arm, than in the --

DR. PROESTEL: The ischemic and the Class IVS were --

DR. KRUCOFF: Were higher in the OPT than in the CRT --

DR. PROESTEL: Right.

DR. KRUCOFF: Okay.

DR. PROESTEL: Did I say that the other way?

DR. KRUCOFF: I'm not sure what I heard or what you said.

DR. PROESTEL: Okay.

ACTING CHAIR LASKEY: All right, this is not a rhetorical question. For this statistician again, my -- when I look at the data presented by the sponsor in these figures, these blocks, the survival curves. There are two pieces of data reported here. The first is the log rank statistic that compares the two survival curves which is the standard way to do product limit survival analysis. And then there's this hazard ratio which comes out of another analysis. Is that correct?

DR. KRASNICKA: Yes, yes, correct.

ACTING CHAIR LASKEY: That comes out of a Cox proportional hazards regression.

DR. KRASNICKA: Yes.

ACTING CHAIR LASKEY: And that's a different set of statistics than the standard product limit Kaplan-Meier set of statistics. And that's I think, part of the confusion up here, is that on one plot both of these, quote "results" are being reported and yet, the problem you're having with the Cox proportional hazards has been well articulated but it's -- I guess the other issue is how we interpret the Kaplan-Meier curves and I guess we'll come back to that this afternoon, but there's two separate analyses going on here.

DR. KRASNICKA: Yes. Completely separate.

ACTING CHAIR LASKEY: Yeah. Thank you. Dr. Somberg, are you not hungry?

DR. SOMBERG: No, not really. I'm on Central Time, remember that. It's not lunch time yet. I'll make it very quick. Number one, I'm going to play devil's advocate for a moment here and the -- while there's debate whether the four-hour infusion was to be counted or not between what we heard of the sponsor's presentation or the academic investigator's, I should say, presentation, and the FDA. Let me ask you, does it really matter, because it only contributed, I think we said four percent?

DR. PROESTEL: Well, basically, we are cataloging the changes to the end point. In fact, the case report form originally was designed to capture greater than four hours from the beginning of the trial, so I don't see that as a problem. I do think that the other two changes to the primary end point are concerning because they occurred during the trial.

DR. SOMBERG: Okay, I hear you, and my other next question is the study withdrawals, that was a very high number, 20, 25 percent and that's what really got the investigators to decide to go back and to reconsent and to go through it. I was very impressed how thorough that was but I understand that comment was made that there's a question of the reliability, that it may be unreliable and may have added a bias into a blind. I mean, isn't that to be commended, to go back and to look at it. If we left that 25 percent and we found that 20 percent difference, then we would have said, "Hey, look, that could have contributed, but now we've gone back. It was reduced to next to nothing and why is there a bias, why is it unreliable?

DR. PROESTEL: Well, there's a number of issues. One is there is an -- if you allow -- that would be, I guess, the fifth change or well, maybe the fourth change. You know, there should be some limit on the number of ways one can reinterpret the design of the trial. And while I certainly agree that this additional information is valuable, I think it's worth considering that the original specified plan should also be presented with that data and this would be adjunctive data that could be included.

Another issue, as far as the reliability, I'm going to try and find a piece of paper. It provides the description the sponsor provided for what was done. You can chat amongst yourselves.

ACTING CHAIR LASKEY: While we're doing that, is Dr. Waldo still with us?

DR. WALDO: Yes, I am.

ACTING CHAIR LASKEY: Great. Did you have any queries for the FDA?

DR. WALDO: I mean, I think this whole discussion of the statistics is critical. I share with my colleagues, I'm not a statistician and I think I have to tell you honestly, when I first read this, I -- my tilt button went off because of all the numerous changes. I mean, the first change was well over a year after into the trial. The second change was still a year later. I mean, that just bothered me but again, I have to rely on my statistical colleagues to say if that's -- something which is intuitive has merit in terms of my being upset. I just think that was really bad.

Of course, I mean, you -- and this -- and we kept hearing that this was -- all previous trials had done it this way. Why didn't they design it that way from the beginning? I think that was a problem. And I think I need some more statistical help.

The other thing that bothered me was that some of the adverse -- some of the things with the implantation of the pacemakers were considered as adverse events because of the way that they were -- with the revised definition. So in other words, if you had a revised lead or something like that and you didn't have to stay overnight in the hospital, that was just an adverse event and it didn't require hospitalization, the reason that really bothers me, again, I notice, I think I heard there weren't that many revisions but I don't know how many other things there were, but what bothers me about that, is that really we've heard over and over again from both the presenters and from the FDA analysis that this whole thing was driven by hospitalizations, I thought 90 percent roughly I think is right, of the events, so hospitalization, I think, is really critical.

And I share a lot of the concerns about how you consider hospitalization because the hospitalization is the reason that you reach the end point in this trial and you make conclusions. So if you just give devices a buy as they seem to have done, I don't think that's valid. It just doesn't make any sense to me. It doesn't make economic sense. I think when you consider all things with patients, they have to understand that you know, that the hospitalization is part of this. So that bothers me also because it's hospitalization driven.

In fact, I'd be honest with you. I was thinking that if I were designing this trial and I'm an electrician and not a plumber, but I would have thought that mortality was a critical part of this and it's not the major driver of the primary end point. And I was even asking -- well, so I'm saying a lot of things. I have two other points. I'm saying too many things before lunch, I think, but I have read many, many times the approved indication and the request for change that Guidant is asking for and I have difficulty sorting out the difference. So, I mean, that's even a more fundamental question for me. What are we here to talk about, because I haven't appreciated the difference between the approval that I understand they have and the change that they're asking for. So that many -- and I have a few other things listed by maybe that's enough to start for now.

ACTING CHAIR LASKEY: Right, we'll come around to general critique comments this afternoon, but I just wondered whether you had any questions for the three FDA presenters but --

DR. WALDO: Well, I only worry about that my relative unsophistication in understanding statistics and I respect the statisticians and I know Dr. DeMets, too, and I think he's a well-respected person, so I wish that the two groups of statisticians could maybe come to some understanding or do we understand there are disagreements between them because I'm not sophisticated enough to challenge one or the other. I do very much worry about all of these hospitalization changes and in a the study driven by hospitalization where that's really what has driven all -- virtually all the conclusions in this trial, that this seems very messy and very worrisome to me.

ACTING CHAIR LASKEY: All right, well, rest assured we'll try and get some consensus for you this afternoon. Thank you, Dr. Waldo. We'll get --

DR. WALDO: Sorry, I couldn't be there. I got to Baltimore, but the plane wouldn't land.

DR. PROESTEL: I'm sorry, just to follow up, we had discussed this issue with Guidant and they provided a response. It's a withdrawn patient consent process and I'd like to just read a portion of this so that you might understand our concern. "Guidant determined that if patients did not withdraw their consent at the time of discontinuation in the trial, they would not require reconsent. Rather they would be covered by the original study consent if the coordinator was aware of the patient's status and did not require consulting the family or medical records. A second letter was sent to the principal investigators on March 6th, 2003 clarifying this information. A copy of this letter is attached for reference".

This letter cites, "to review their patient's consent status from the patient device status form attached, if the withdrawal reason selected was either 13, patient refused follow-up or possibly 88 other if explanation given indicates consent was withdrawn. The situation would require reconsent with the additional informed consent as outlined in the February 20th, 2003 letter". This is the important part. "All other reasons for withdrawal would allow the research coordinator to fill out required CRFs including withdrawal contact and treatment modification if patient received his device if data was known without contacting the patient, family or medical records".

So to me this indicated that data was being filled in to CRFs based on memory which I think is unreliable.

DR. SOMBERG: I mean, I hear what you're saying but I'm not sure that states that. It says that they would fill out the CRFs if they didn't feel that it required a secondary consent form filling because of those two issues. If a data coordinator fills out a CRF, and we can ask the group here that monitored the studies, they would have to go back to the source records. I mean, I do investigations all the time and my brain is zilch for remembering what happened yesterday in terms of all sorts of things because you hear a constant in-flow of data so you go back to the source records. So I don't think there's that implication there because I think that goes to the heart of the matter is the changes and, you know, I grant you there may be, and we can have a debate on this and all that but if there were changes, does it increase the unreliability and I thought going back and reconsenting and going down to only about four patients that were not in the data base was a remarkable success from a potential failure of having 20, 25 percent not filled in. So I think we should go back after maybe lunch and see if it was just on guesstimates on what the data was or the data coordinators were actually instructed at each site to use source records and did they not get monitored and have the source records checked.

ACTING CHAIR LASKEY: I don't. So do we have access to that, what you just read? Maybe you could make some copies for us. It's somewhat at odds with what Dr. Bristow described the process as being, so it would just be helpful. I'm really suggesting that we break for lunch at this point. I have 12:40. Let us regroup at 1:40 and we'll resume. Thank you very much.

(Whereupon at 12:40 p.m. a luncheon recess was taken.)

A-F-T-E-R-N-O-O-N S-E-S-S-I-O-N

(1:45 p.m.)

ACTING CHAIR LASKEY: All right, people, thank you for coming back on schedule. It being 1:45, I'd like to resume and before we have our lead reviewer give his review, the FDA had one more point to clarify something that came up during our conversation with Dr. Waldo.

DR. FARIS: FDA would just like to offer clarification on one important point that was raised. Dr. Waldo asked a question about the significance of the population change in the indication statement. The sponsor's current indication requires that a patient meet the specified heart failure criteria and also have a conventional indications for and ICD. The sponsor is seeking removal of the ICD indication requirement based on the COMPANION results.

DR. WALDO: Thank you.

ACTING CHAIR LASKEY: Welcome back, Dr. Waldo.

DR. WALDO: Thank you.

ACTING CHAIR LASKEY: All right, we'll start out with Dr. Maisel giving his review. Bill?

DR. MAISEL: Thank you. Good afternoon. I will not review in detail any of the data that has been eloquently presented by both the sponsor and the FDA and I think many of the important issues have already been touched on. I would like to focus on a few of the contentious issues which, in my mind, include a few things. One is the hospitalizations. Second are the withdrawals. Third is the mortality end points and then finally I'd like to talk about some of the safety issues. So I will start with the hospitalization issue.

Just as a point of clarification from the sponsor, I'm interested in understanding exactly what it was that prompted the changed in definition of the hospitalization end point. One quote I heard this morning was to make verifiable data possible. So is it your position that the reason the hospitalization end point was changed was so that the data could be interpreted correctly that you were receiving in the case report forms? It's a yes or no question.

DR. CARSON: The answer to that then is, yes. The -- once again, to reiterate and maybe I can just amplify this because it keeps coming up, maybe amplify a little bit more what was said this morning, the -- for every trial in which hospitalization has been used in heart failure as a primary or secondary end point there's been a duration criteria. The duration criteria has not always been stated in the protocol. It wasn't stated in the VALHeFT. It was stated in the MERIT Heart Failure protocol but then the committee went to a calendar date change from a 24-hour. I'm sorry.

DR. MAISEL: I understand -- you can stay there. I understand a lot of those issues and I don't want to rehash them. What I'm trying to understand is, you also said that you felt that events that were less than 24 hours in duration were, "exceedingly rare". So I'm trying to understand if you felt that those less than 24-hour hospitalization events were exceedingly rare, why you felt so strongly about changing the primary end point which obviously has led us to a great deal of --

DR. CARSON: Discussion.

DR. MAISEL: -- discussion.

DR. CARSON: First of all, I would say from my standpoint, the standpoint of the morbidity and mortality committee, on the steering committee, the end point did not change. The end point committee, in a sense, finalized the criteria for "all-cause" hospitalization by presenting a 24-hour barrier. That was, in part, because it had been done in previous clinical trials to that time and also it represented a day in the hospital and I think as everyone is pretty well aware, many hospitalization systems define a hospitalization as being something over 23 hours.

Now, what I said this morning was that a calendar date change, hospitalizations that did not involve a calendar date change, I believe, are rare and a little difficult to figure out what they would be. So 24-hour -- less than 24-hour hospitalizations are not necessarily rare. In fact, in this trial, and we have a backup slide on this, I think about 16 percent of the patients in CRT-D had a hospitalization for less than one -- than a 24-hour period. About 20 percent in CRT did. So there --

DR. MAISEL: And what about OPT?

DR. CARSON: I'm sorry, 20 percent in OPT and 16 percent in CRT.

DR. MAISEL: Okay. I guess, my point simply is that while it seems that your intention was to make it easier to interpret the end point, I think you added a great deal of confusion and I think the simple was the patient hospitalized or not, while I understand the issues regarding whether that was the appropriate end point to pick, it was picked and I don't agree with the position that you clarified things by changing it. I think it obviously, in my view would have been a lot easier just to count how many people were hospitalized as was initially intended. And I'll give you a chance in a minute to respond to that.

DR. CARSON: Okay.

DR. MAISEL: The other issue I had was I'm trying to understand exactly when it was that hospitalizations were first adjudicated. There's a statement in Section 6-1 on page 4 that says, quote, "No hospitalizations were adjudicated until the 6/23/01 meeting". Is that accurate?

DR. CARSON: That's incorrect. That's not correct.

DR. MAISEL: Okay, so were they first adjudicated in March 2001?

DR. CARSON: The first adjudication meeting was March 16th, 2001.

DR. MAISEL: So is it fair to say that the data was not analyzed or looked at until those events were adjudicated? What I'm trying to understand as well is that in Section 5-4 on page 14, there is a graph of the DSMB analysis. And the first point where there is an analysis is dated November 10th, 2000 and it says, "combined mortality and hospitalization end point", and it has a Z statistic. So I'm trying to understand how they were able to analyze the end point prior to any end point adjudication, if you could clarify that for me.

DR. CARSON: I think that would probably be a question for -- one would say then that what they were looking at was unadjudicated data for the primary outcome. That would have been the only way that could have been done because we did not meet until March 16th of `01. That was the first time -- the first meeting we had and prior to the start of that meeting and let me emphasize again, prior to any end point ever being adjudicated, the 24-hour duration hospitalization was in place.

DR. MAISEL: So the earlier discussion we had this morning where it was stated that the data went to the M & M committee and then back to the clinical research organization and then to the statistician and then to the DMSB was not necessarily always the case.

DR. CARSON: Well, the adjudicated forms, the adjudication data, would have gone to the M & M committee. The adjudication data would have been adjudicated by us. Whether there was another communication of unadjudicated data, maybe Dr. DeMets could tell.

DR. DeMETS: Yeah, the thing is quite common in monitoring trials and groups like mine. It would be reports for monitoring, that is you take what you have, the best most up to date data you have, so at that point in time, you're correct M & M committee would not have met but we clearly had data on unadjudicated events, mortality and so you typically present the best data you have, which is a mixture along the way of adjudicated, unadjudicated, at that point in time was all unadjudicated, and as they move along, you have a mixture of adjudicated events and plus the non-adjudicated and then you'll probably -- we always do, at least at our place, provide a table which has got the adjudicated, but that's always behind.

So while it's adjudicated, it's old news. So -- but we were looking at what the team was looking at which we reported to them at that point in time would have been unadjudicated, but they would have seen that or known that.

DR. MAISEL: Right, but my obvious point is that I'm concerned that there was statistical analysis that was performed prior to the changing of the definition of hospitalization and if you look at the Z statistic, it's in favor of the OPT group. The Z statistic is minus 2.057. If you go to Section 5-3, page 42, you show the DSMB same analysis for "all-cause" mortality and the Z statistic favors the device. And so what that says to me is that the negative Z statistic was strongly because of a large number of hospitalizations in the device group. And so this was known as of November 2000 and so it just begs the question of you know, five, four months later now, there's a meeting to discuss changing the definition and while I certainly understand and respect the statements that have been made that there's no communication, et cetera, you know, on paper it seems that the fact that there were a lot of hospitalizations in the CRT-D group early on, was clear at the time of that, that the definition was changed.

DR. CARSON: Could I just maybe help with one comment here? Recall that what the sites were being requested to send were events that from the original CRF that had a date change. So, in fact, all of those hospitalizations then would have come to the external CRO. There would not have been an additional group of hospitalizations. Those hospitalizations all then eventually came to us after they assembled with all the clinical materials that would make it possible for us to have an opinion on each case.

So Dave, I think that would be --

MS. WOOD: If I could interrupt for just a minute, just a procedural issue, the tables should be left free. If you have a question to answer, please come to the podium. That allows the advisory committee to interface with both the FDA and the sponsor. Thank you.

DR. DeMETS: I apologize for my lack of protocol. Yes, there was no communication. In fact, we followed almost to the letter the current independent monitoring committee charter, draft charter, that was issued in November 2001 to alleviate just the kind of concerns that you are pondering. That is by having an independent statistical center, an independent monitoring committee, an independent M & M committee which did not communicate those kind of concerns are to be addressed in that way. So that's why the FDA charter was written that way. That's why it's been conventional practice for the past 30 years, I suppose. So there was the communication to prevent those kind of issues being an issue.

DR. MAISEL: Okay, thank you. It was also -- it was stated in the FDA review but I'm not sure I saw it in the sponsor review, that it was not possible to go back and analyze the data based on the initial definition of all hospitalizations, recognizing that the implant hospitalization was not going to be included. Is that an accurate statement, that you do not have the data on "all-cause" hospitalization putting aside the device implants? In other words, hospitalizations that were -- any hospitalization, the original definition in the protocol.

DR. CARSON: Well, there would be -- what we don't have particularly from my standpoint, Dr. Bristow may have something to add, but there is not data in which there was not -- the sites were asked to report according to the case report form and that involved a calendar date change. So there is -- there's not data then on hospitalizations who did not meet any sort of duration criteria.

DR. MAISEL: Because it was stated this morning that -- and I believe it's on one of the forms that it says, quote, "You must use this form for each hospitalization". So was that -- were you -- I mean, if I were doing it, I would have tried to collect as much hospitalization data as possible and then if you were going to narrow the scope, I understand that, but it was stated this morning that the participants were asked to submit a form for every hospitalization. Is that not true? They were asked to adjudicate the event themselves and only submit the form if there was a hospital date change or they submitted a form for every hospitalization?

DR. BRISTOW: Only if there was a hospital date change did they submit a form. Let me provide a little background here in terms of the "all-cause" hospitalization notion so -- on June 17th, 1999, we met with the FDA about the thoughts for this protocol and the concept was that we would be running a clinical end point that would include hospitalization and death was a competing risk. And some discussion took place with the FDA regarding what that hospitalization would be.

Our notion, and I'll give you some direct quotes here, I brought the wrong thing to the podium, unfortunately. My direct quote though was something like a real hospitalization in fact, DRG 127 for heart failure and so our original notion was that we were going to run a competing risk, primary end point of death and heart failure hospitalization or at the least, cardiovascular hospitalization because this is the hospitalization component that can be benefitted by an effective heart failure treatment.

So the idea was that we have a real hospitalization, not something where somebody's blood pressure is found to be 120, not 60 or his INR is found to be two, not seven and then gets discharged right away. This study would count real hospitalizations, DRG 127 including heart failure. So right from the beginning, the idea was to eliminate these trivial things that could happen, use of hospitalization for short stay, for example, real hospitalization and then the notion of "all-cause" actually came from the FDA.

They said, "Well, fine, you know, measuring heart failure, cardiovascular hospitalization is okay, but we want you to measure all real hospitalizations. We want you to capture the stuff that might be a fallout from device use and implantation. Okay, if you have a complication of a device requiring a hospitalization, subsequent hospitalization, we want that captured".

And so we agreed, "Okay, we'll do this". Now, this is not ordinarily done in a heart failure clinical trial because you're dragging along a lot of noise. In our case, about a third of the total hospitalizations were non-cardiovascular and were not going to impact favorably on that with a heart failure treatment, but because this was the mandate from the FDA, this is where "all-cause" comes from. Spreading out the mode of hospitalization, the cause specific aspect beyond cardiovascular or heart failure into non-cardiovascular, it never met stuff that really isn't a hospitalization. It doesn't really require a hospitalization and we can track this back historically.

So of course, what happened in COMPANION is we had a much greater treatment effect on cardiovascular hospitalization. In fact, the hazard ratio is something like --

ACTING CHAIR LASKEY: Thirty-six percent.

DR. BRISTOW: No, it's not quite that. It's .72 and for heart failure hospitalization, the hazard ratio is .6. So the total comes from measuring non-cardiovascular hospitalizations.

DR. MAISEL: I don't debate the well-meaning or potentially even the appropriateness of the definition that you ultimately ended up with. I think there are a couple of important points. Number one is a device trial is not the same as a heart failure pharmacologic trial obviously. Number 2 is, I'm still a little unclear as to why this conversation that took place in March 2001 didn't take place in 1999 when the protocol was written and maybe you can shed some light on that.

DR. BRISTOW: Frankly, I guess I can take some of the credit for this. The steering committee and myself specifically, never thought this was a substantive change. This is the technical way the end points committee does its business and this is the way that I have handled it as a steering committee member previously. We let the end points committee decide how they're going to do things. They do state of the art things. They tend to be the same people from trial to trial and to me, this really never made any difference. They had to use a system that would allow them to have a verifiable real hospitalization in the spirit of the protocol.

To me this was technical detail as opposed to a substantive change in the primary end point. That is the reason why we didn't basically say, you know, "Sponsor, you've got to tell the FDA blah, blah, blah". We just never thought that this was anything substantive.

DR. MAISEL: Okay, I'd like to shift gears a little bit and talk a little bit about the withdrawals.

DR. CARSON: Can I just answer one more thing because you brought it up at the beginning of this question and that was the fact that the end point duration was 24 hours and then it was a calendar date change. I just wanted to re-emphasize that this was done because the data that was being collected on the case report form was a calendar date change. When the committee looked to try and pull out to verify that these were 24-hour admissions when it was a single calendar date change, we could not verifiably do that. And that's why we made that switch.

DR. MAISEL: Okay, thank you. It's been well-documented that the withdrawal rate was much higher in the pharmacologic, the OPT group compared to the CRT groups and I think we all recognize the reasons for those withdrawals regarding implantation of CRT devices. I guess I have a couple comments and then you can respond. Number one is, it seems obvious to me from reading the instructions to investigators that that was going to result in a large number of withdrawals, I think, forcing physicians to get approval to do what is a medically indicated procedure in a patient, I think would automatically result in withdrawal.

So did you consider -- I mean, to be what I probably would have done was simply given them very specific instructions about who could get a CRT device. Essentially, it seems to me that they were -- physicians were forced to withdraw their patients if they wanted to do what was right for their patient.

DR. BRISTOW: Well, you have to understand that the withdrawal rate began to go up when these devices became on the market and then we sort of reacted to this emerging problem that we had. And you know, the truth of the fact is that we had not proven that either of these devices works in this patient population. And our position was that if you're an investigator, you ought to have that report about the treatment in your trial and this is unproven therapy and you really shouldn't be doing this.

But, yes, there comes a time and just for patient care, if you have an approved something but there is what has to happen. There really has to be deterioration and it has to be documented. We felt that was a reasonable way to do things. So, what would happen, of course, as has been mentioned earlier, you know, the patients that were withdrawn probably were the ones getting sick. And, of course, if they're withdrawn and we never find out the end point, that's going to work against the device. On the other hand, we don't know -- as someone else mentioned, we actually don't know how this is going to work out. So the ethical mandate is to go get all that data.

DR. MAISEL: Yeah, I think you should be commended for an extremely thorough and difficult job of filling in the blanks for all those withdrawn patients and certainly had you not done that, I'm sure we would have spent a lot of time discussing that today. I'm a little bit concerned about how the missing data, particularly in the hospitalizations, what's filled in. There's some patient scenarios given in Section 6-2 on page 4 and one example is that, you know, a patient is contacted by phone and reports that they had not been hospitalized in the last whatever it is, 18 or 19 months and that was accepted as, you know, data and an end point, and I think we can all recognize the inherent unreliability in data like that.

I'm concerned about that, more for the hospitalization data than for the mortality data. What efforts -- I think if a patient -- well, maybe you can clarify for me. If a patient denied being hospitalized, they got marked down as not hospitalized and if they said they were hospitalized, the data was tracked down; is that --

DR. BRISTOW: Oh, yes, absolutely. I mean, the only risk from this, I believe -- I mean, the same procedures were undertaken as for non-withdrawn patients and the only risk here is that you would have under-reporting. You just wouldn't be able to get all the events, in which case, that would lead to a lower event rate in the disproportionate withdrawal group, which would be the OPT group. Again, the bias would be against the device.

But we -- I mean, the coordinators, investigators were instructed to go get these data. They had to have source documentation. This had to be adjudicated, had to have the dossiers filled with all the source documentation and so forth. So it was handled exactly the same.

DR. MAISEL: So, I guess to summarize my position on the hospitalization, I would say I'm quite concerned about a number of these issues, perhaps any one of which may have been possible to overlook but the data analysis prior to the initial adjudication, the large number of withdrawals, the unreliability of the data makes me concerned about interpreting that end point as well as if you step back and ask the clinical question, you have a patient in front of you. You know, in my mind the initial hospitalization, while I certainly recognize the goal to demonstrate efficacy of the device, taking a step back, you know, if I have a patient in front of me and tell them that they're going to be hospitalized, I think there's no conclusive evidence that that's the case here.

DR. BRISTOW: Well, another point is, it's not just hospitalization that you're effecting, heart failure hospitalizations primarily, but some other cardiovascular perhaps. With that goes improved quality of life, improved exercise tolerance, all the stuff that relates to interrupting the cycle of progressive heart failure. We haven't presented any of that data because that was used for previous approval of the device. But it's not just the hospitalization, it's everything that goes with progressive heart failure is benefited.

DR. MAISEL: I completed agree with what you just said. With regard to the mortality end point, I'm comforted by the statistical analyses that have been presented today. I think in the log rank or Wilcoxin statistical evaluation whichever you prefer, both demonstrated in an unadjusted analysis that mortality was improved in the CRT-D group. I recognize the shortcomings of the Cox proportional hazards analysis but that also showed a benefit.

I'm more comforted by the withdrawal analysis of mortality simply because I think it's much easier to identify vital status. So I do believe that these devices do result in improved survival and decreased mortality.

DR. BRISTOW: In regard to that, I certainly agree with that comment. The original protocol actually gave some guidance for going after patient's mortality data, vital status data, who had withdrawn. It was in the protocol and what we added, really to that was to go after the primary end point data as well, and we totally agree that the mortality date is undoubtedly more reliable in the sense of getting the data out on a withdrawn basis.

DR. MAISEL: One of the questions that we've been asked to consider is whether we can consider the mortality data in isolation or whether it should be part of a further analysis and I agree with your comments that the sub-study certainly suggests that the New York Heart Association class improves, 6-Minute Walk improves, Minnesota Living with Heart Failure, Quality of Life improves. I think there is evidence that the device is improving heart failure symptoms. I'm just not convinced about the hospitalization piece.

Finally, I'd just like to touch on safety and I'll stop in a couple of minutes. I do not agree with what was listed as the primary safety outcome, which is complication in patients that were successfully implanted. I think for obvious reasons, this leaves out attempted device implants which have relevance to device safety. If we consider an extreme example. If 90 percent of patients die getting a device implant and the 10 percent who got it had not complications, your report would list 100 percent, you know, safety and zero complications. So do we have data on the patients in whom events were -- devices were attempted but not implanted regarding their complications, and perhaps data on that quote "Primary safety outcome" but for complications in patients who had an attempted --

DR. SAXON: Right, so you're right, the systems safety definition is -- it's an FDA convention established in 2000 is the narrowest definition because it only includes complications and serious things in patients that were actually implanted. The system safety shown on the right here is the issue that you're interested in. This is more encompassing. This is all randomized patients including unsuccessful attempts. This not only counts those more serious complications, but also includes any observation. So I believe that's the answer to your question.

DR. MAISEL: So if I read that correctly, there was a very small number -- the rate was essentially the same in the -- of the complications of the attempted patients.

DR. SAXON: Correct.

DR. MAISEL: Okay. And then finally in the tables that are presented both in the labeling and in our submission, there are times when the numbers don't add up such as there might be a certain number of complications, a certain number of observations and then the total number is not the same. I can give you an example, the phrenic nerve/diaphragmatic stimulation, there were eight listed complications and 52 observations but it says the total is 58 and those sorts of discrepancies appear in multiple places. Can you explain why that is?

DR. SAXON: Right, so some of the things that you think of as being consistently related to the LV lead actually aren't. Some of them are related to the RV lead for instance, so that would lead to a miscount. Some can be counted in both bins because you can have phrenic nerve stimulation that can either to away or need or not need a programming change or an intervention to correct. Or you can have new phrenic nerve stimulation that wasn't initially counted.

DR. MAISEL: So there can be the same event in multiple patients, I understand. Well, why don't I stop there. I'll let some of my colleagues fill in some of the blanks?

DR. BOEHMER: Could I possibly interject something about hospitalizations? Your concern was the total hospital burden to the patient, not necessarily being represented by "all-cause" hospitalization.

DR. MAISEL: I would say that is a -- stepping back from the trial, that is a clinical -- a question I have as a clinician analyzing the data or looking at the data.

DR. BOEHMER: All right, well, as a clinician that takes care of a great number of heart failure patients -- by the way John Boehmer, Penn State College of Medicine. My conflicts are as a consultant for Guidant Corporation and investigator and some reimbursement for travel here.

This is hospitalization rate by months. Now, when I talk to a patient about getting a device, they understand that they're going to get a device. And I will need to explain to them that they're going to get the device in a hospital, but what happens -- but if I'm going to tell them that it's going to decrease their risk of hospitalization, they're not going to be confused about the fact that they're going to go in the hospital and get a device. What they want to know is, "What happens after I get the device", and this is all hospitalizations. This is nothing held back and the skill doesn't help it a great deal because they have to show the initial hospitalization for all the patients randomized to CRT-D but immediately thereafter there's a drop in the rate of hospitalization. That's maintained until you get laid out in the trial when you start getting into issues of who's left in the trial because there is a survival differential.

And I think just the quality of these data are reassuring to me when I would be talking to a patient. I would never suggest to them that they're going to magically get this device without going in the hospital. That would be unreasonable. Additionally, as things evolve, maybe they won't have to go in the hospital as much. Maybe the techniques will get better, maybe the care of them will get better. In fact, this is already a moving target. So I think this way of looking at the data and the way we actually did it in the trial to give us a pass on the initial hospitalization which was in the protocol, I think this is the way a patient can understand it. Thank you.

ACTING CHAIR LASKEY: Now that you've put up that confusing graph to me, there were twice as many patients in the CRT-D as in the OPT so could you go over the Y axis on this, please?

DR. BOEHMER: I'd be happy to. Those are rates of hospitalizations; hospitalization rates, number of hospitalizations over number of patients at risk in any given time point. So the denominator levels it out.

ACTING CHAIR LASKEY: So it is divided by two.

DR. BOEHMER: Uh-huh, it's divided by the number of patients at risk at any given time.

ACTING CHAIR LASKEY: Thank you. Okay, let's attempt to confine our comments to 15 minutes each, if possible, and we'll start with Dr. Kato, comments or questions.

DR. KATO: Well, a question for the sponsor; you mentioned that a number of patients had in the CRT-D cohort, dysetinaria (phonetic)sepsis. I guess there were 10 deaths there and five in the CRT-P cohort. Can you explain a little bit more about the sepsis? Was this related to the device?

DR. SAXON: You're correct, there were a number of septic deaths and I can just -- there are enough that I can go through them with you. They're not clearly related to the device implant either temporally or looking at the clinical history. For instance, there's a leg cellulitis that was thought to have a history pre-operatively. There was an acute appendicitis, a PIC line dialysis issue, septic shock in a dialysis patient, not an uncommon event, cellulitis proceeding to an osteomyelitis, substance and setting of renal failure.

One issue that may have temporally been related to the device, although there was proceeding phlebitis or potential prostatitis, colitis. So the vast majority of these events were not clearly related to the implant and could be attributed to another morbid event.

DR. KATO: Thank you. One other question is, you know, in the final assessment looking at a CRT-D versus CRT-P, do you -- you know, what do you actually think is the final reason, if you can summarize in a couple sentences why the CRT-D does better. I mean, is it just that they are being paced and then they're defibrillated or whenever they go into that rhythm and that's their final safety net or do you have some other hypothesis or actual data behind that?

DR. BRISTOW: I think what we can stand behind is there is a reduction in sudden death in the CRT-D group compared to OPT. There's not in the CRT-P group and that might be expected, obviously, from the ICD component. So the ICD component is adding a reduction of sudden death. Both devices are reducing pump failure deaths and then additional reduction in mortality by sudden deaths. So if you look at mortality or a composite, including mortality, although it's washed out by hospitalizations for the primary end point, the CRT-D is obviously doing better for mortality.

DR. KATO: Is there any data that you could obtain from the interrogation of these devices after the patient dies or certainly in the CRT-D group, is there any interrogation data?

DR. BRISTOW: We have no interrogation data to share with you today. We're in the process of rounding that up but we don't have any. We do have appropriate device firing data which Dr. Saxon could review with you, if you'd like which is consistent with this device in other settings, other trials, and so forth.

DR. KATO: Well, then in the CRT-D group, I mean, how often did the device fire?

DR. BRISTOW: I think it was 11 percent of patients at one year and 19 or 20 at two. We can give you the exact data.

DR. SAXON: Now, while we don't have the deaths, we have the interrogations that we think are relatively reliable from the centers for appropriate chalks and that certainly looks like 11 percent a year and around 20 months at 19 percent for VT or VF therapy.

ACTING CHAIR LASKEY: One question, I hate to keep bringing up this hospitalization issue but I guess one of my question is, if you couldn't identify the time of the admission and discharge and you have to resort to the change in calendar date, which is actually a typical method for hospitals, even hospitals to determine whether somebody is hospitalized or not, how could you determine whether the patient was on intravenous pressor support for four hours?

DR. BRISTOW: I'll actually ask Dr. Carson who reviewed these data as the adjudicated. There obviously, was a special form that was filled out, the IV infusion form. He'll give more color on that.

DR. CARSON: Yeah, I think that's correct, there was a separate form that we tried -- it was a follow-up case report form. This was what I showed on the -- on my formal remarks, presentation this morning. It was that form that was filled out by a site that would give the exact times of intravenous infusion of an inotrope or vasoactive agents. As I said, the sites were not asked to provide the information on discharge times or admission times. We could find admission times pretty clearly in charts, but we could not really find discharge times in most patients and I think the discharge time, as you know, is subject to some variability relating to social issues as well as medical issues.

DR. KATO: Right, but I mean, so that when you're doing an infusion time, there's no -- you didn't record the start and stop time. You just said the --

DR. CARSON: We asked the sites to provide that information on this form. We did ask them to do that.

DR. KATO: And so they could do that but they couldn't do the other --

DR. CARSON: Well, they were not asked to provide that data.

DR. KATO: Okay. Thank you.

ACTING CHAIR LASKEY: Dr. Yancy.

DR. YANCY: Thank you, Warren. One question briefly and then a few comments. And it pertains to one particular graphic shown in the FDA analysis and it's specifically the FDA analysis when we tally the secondary end point and it shows sudden cardiac death event rate per 100 patient years and numerically, at least the CRT-P group has a higher sudden cardiac death rate. The question is, is that a statistical blip or do we think that that's an issue that needs further thought?

DR. BRISTOW: Is that addressed to FDA?

DR. YANCY: Whoever can answer that, if it's FDA or if the sponsor can --

DR. BRISTOW: Well, since you're referring to the FDA analysis, why don't we allow them to comment, then we'll respond?

DR. PROESTEL: Well, it was a concern that had been brought up actually to us through public presentation. So we were curious to know in the CRT group what was going on with sudden cardiac death. I think for the purposes of the CRT-D device, the FDA can say that we were reassured that in fact, pump failure death overwhelmed that increase in sudden cardiac death. I mean, there's a number of reasons why we should be skeptical about that sudden cardiac death blip. It's obviously, a sub-group analysis. It was not pre-specified. There is the issue of competing risk. You know, so what I would say is that for the purposes of the CRT-D device, we were reassured that in fact, "all-cause" cardiac death as well as "all-cause" mortality was improved in the CRT arm. And you know, it was -- as far as statistical significance, I wouldn't calculate P values for those.

DR. YANCY: Well, that's my reason for bringing it up because I think that right now the record from this morning's discussion states it was increased and I don't know that we can say that comfortably and I would not want that to stand as a matter of fact.

DR. PROESTEL: That's correct. These were really point estimates.

DR. BRISTOW: We agree with that and, in fact, if we can just show the Kaplan-Meier curves and so this is sudden death Kaplan-Meier curves and basically there's no statistically significant difference between A and B, which is CRT-P and OPT, the P value of .495.

DR. YANCY: Thank you. Warren, my comments are more along the line of my perspective as a clinician who does this kind of activity on a day to day basis. And I don't know if this is where you want me to speak to that or not but I think it's germane to the discussion we've been having. And the first thing I would say is with regard to the implication of hospitalization, not all hospitalizations carry the same weight and in the context of a heart failure patient, a heart failure hospitalization carries with it an extraordinarily high incidence of rehospitalization and a 12 months very high rate of mortality and so I think that if there is even a signal that the hospitalization is impacted as a practitioner who takes care of desperately ill patients with this condition, I think that signal needs to be respected.

But I think even beyond that, as someone who actually helps participate in the writing of guidelines that govern how heart failure medicine is practiced across the country, there is pressing need to have clarity on where this technology resides and I think for whatever worts we may have uncovered, this is the best data base we have right now for patients with advanced disease who are at very high risk for serious events hospitalization and death and so in my judgment, I would want to go on record publicly for commending the investigators for working with a difficult patient population and bringing together important data and I think that even though we may quibble with some of the definitions, and may have to wrestle with how this was dealt with statistically, I honestly believe what I've heard so far is gymnastics and not substantive and I would rather accept the implications as they are. So I have no further questions.

ACTING CHAIR LASKEY: Dr. Brinker?

DR. CARSON: Pardon me for a moment. Dr. Laskey, could I just make one clarification on the response to Dr. Kato? I just didn't want to confuse the issue of what you were asking because I think there was some confusion in the morning between the four-hour inotrope infusion and the hospitalization criteria. In terms of events that were in the primary end point, hospitalizations were "all-cause" with a duration criteria. They did not require four-hour inotropic use of anything. That was an outpatient end point to be considered part of the primary end point.

And in the response I gave to you earlier, we actually did not attempt to necessarily capture whether an infusion was four hours or later during the hospitalization except as part of the morbid end point but it was -- except to count as one of the morbidity criteria. The form that we used particularly was for the intravenous therapy as part of the CRF for the morbid end point but it was the outpatient end point that was particularly at issue.

ACTING CHAIR LASKEY: Jeff?

DR. BRINKER: I just have a few questions. Have you tracked changes in medications level between the two groups and in fact, whether --

DR. BRISTOW: Yeah, we have and we'll show you some data there.

DR. BRINKER: While you're getting that up, one of the concerns I have is that there's an implication in somebody's reviewed this packet, I don't know who I can attribute it to, that the device group had a higher incidence of hypotension dehydration thought to be due to the maintenance of a medical therapy coupled with the beneficial effects of the device resulting in an over-medication state, if you will.

And I'm not going to argue that point at all because that would be a good end point if such occurred, but what I really want to make sure is that one group or the other perhaps had a decreased hospitalization rate because of medication change.

DR. SAXON: So patients did have an outpatient follow-up, but it is true that in some patients who have this well-described dramatic dieresis improvement in blood pressure with the onset of resynchronization therapy need to be followed particularly if their medication is not adjusted and, you know, it's very difficult to typically adjust it or know how to adjust it. So I would state that, yes, it is a possibility that a dramatic improvement in the systolic response would cause a marked dieresis that could potentially in some patients lead to an event like that, but I would suggest that the patients were tracked in such a way that that was probably a very rare occurrence.

DR. BRINKER: Just out of curiosity, are you suggesting there should be a caution in the labeling? Are you suggesting that --

DR. SAXON: No, I guess I'm responding to your question, could you theoretically develop and I would say, yes, you could. You could -- if you were, for instance, requiring more diuretic dosage, you had an improvement in your clinical condition --

DR. BRINKER: We don't have any evidence of that.

DR. SAXON: -- there's no data that indicates that that --

DR. BOEHMER: Just one piece of data, one piece of data that we do have, we do have ACE inhibitor and Beta Blocker doses over time. The ACE inhibitor doses are in an Alaprol (phonetic) equivalence. If you saw a substantial number of patients with significant volume depletion you would expect two things to occur to them. One is that they would become hypotensive. The second is that they would become asotemic, both reasons that clinicians will obviously respond by reduction in doses of ACE inhibitors and this is over the 12 months of the trial with every time point, including the one week and one month time point and there's not even a blip.

DR. BRISTOW: And so with regard to the Beta Blocker data, the majority of patients were on Carvedilol. It's a lower set of curves. OPT actually has a slightly higher average, daily Carvedilol does throughout the trial. I don't know if that's statistically significant. You can see the absolute difference. And then a minority of patients are on Metroprolol and these are very small numbers as you get out there with OPT in particular, 17 at the end, so there's no consistent change in Beta Blocker dose and baseline Beta Blockers are exactly the same.

DR. BRINKER: So what I might have expected is a change if not a decrease in medical therapy in the device group and increase in the drug treatment group and maybe we're missing diuretic therapy.

DR. BRISTOW: Well, the idea is there patients were maximally treated when they were enrolled, background medical therapy. There was nothing else for them to go on that had any proven benefit in heart failure and they were on everything at supposedly the target doses that they should be on and so one answer is, there was no room to maneuver it in an upward direction at least.

DR. BRINKER: My experience is there's always room for Jell-O. There's almost always some manipulation that can go on. Maybe that did go on in terms of some diuretic or maybe even in the other group in intravenous therapy.

DR. BRISTOW: Perhaps, but, you know, these are chronic heart failure patients taken care of by heart failure physicians, physicians with at least an interest in heart failure and they were well treated coming in and they were well treated throughout the trial.

DR. BRINKER: This next question I have is a little bit of a variation of the one I asked you before. And after thinking about it, I might not have asked you the complete question. That is, do you have difference in hospital burden maybe best described in total days in the hospital in the two different groups rather than admissions and durations averaging?

DR. BRISTOW: Total days. Somebody grab that data. I don't think we have it on backup but we do have a text of it. I can tell you the hospital duration of the two groups because I gave it to Dr. Somberg earlier. So the average days in the hospital which is what I gave him, 8.6 days on CRT-D and 10.9 on OPT, this is of the hospitalizations, the average days in the hospital. Total number of days -- is that normalized to size of the cohort? Well, that's double so that doesn't mean anything. We don't have the data normalized to the size of the cohort for total number of days.

So the best thing I can give you is what I just gave you, the duration of the hospital --

DR. BRINKER: Would you agree, however, that a better indication hospitalization burden is the total number of days rather than -- assuming there's a meeting rather than --

DR. BRISTOW: Yeah, I would agree with that within the hospitalization measurement or the hospitalization event by itself, the most sensitive measure is probably the total number of days. One could argue, it should be the total number of days per patient, obviously which we just gave you. On the other hand, remember you've always -- in a trial like this where mortality is being effected by one -- by the treatment, you have the issue of competing risk and so if you're an OPT patient and you're dying with a higher incidence, you can't be hospitalized. So that's always an issue in these hospitalization data which in and of themselves or by themselves, I think need to be taken with some caution.

DR. BRINKER: My final question is, how many patients left the pharmacologic arm because they developed criteria for a defibrillator. In other words, how many people got a defibrillator alone?

DR. BRISTOW: Okay, not many but we'll give you the real number.

DR. BRINKER: Two.

DR. BRISTOW: Something like that. Two, okay, yes. That's it.

DR. BRINKER: So interestingly, all the other people left for presumably CRT-D.

DR. BRISTOW: Uh-huh, right.

DR. BRINKER: Okay, thank you.

DR. BRISTOW: There were CRTs as well. We'll give you the actual number.

DR. BRINKER: That's close enough. I don't want to burden you.

DR. BOEHMER: Well, interestingly, there were a substantial number of patients in the OPT group that were withdrawn and not implanted with anything. As you can see here, the total number withdrawn were 80. Thirty-one received CRT-P which was the first device approved in the course of the trial. Eleven received CRT-D and two received an ICD, giving you a total of 44. About half the patients withdrawn did not receive anything.

ACTING CHAIR LASKEY: Well, then where did they go? Did they just die?

DR. BOEHMER: It's, I suppose, a common circumstance in a clinical trial that the group not doing quite as well ends up either withdrawing or stopping therapy at a higher rate, so those might be explained in that regard. Not everyone was withdrawn to receive the device. That's the important part. It might be -- you know, in centers such as mine, people travel a long distance to come see me and if they ended up in a control group and the ride kept getting longer and longer and the winters kept getting smellier, they may not come the next time and withdraw consent.

DR. BRISTOW: But to answer your question, some were end pointed. We showed some data about the number of end points we got out of the withdrawn patients. Some were not end pointed and we were able to follow them till December 1, 2002 and others we could not ascertain, so it was sort of a mixed bag in terms of what happened to them.

ACTING CHAIR LASKEY: Good. Thank you. Dr. Normand.

DR. NORMAND: Okay, I have a few detail-oriented questions and then some general questions. And so the first question I have has got to do with -- and I know I'm going back to the beginning but inclusion and exclusion criteria and I just am not understanding something and it's probably pretty obvious and that is I think people had to be hospitalized for heart failure within the previous 12 months was an inclusion criteria.

DR. BRISTOW: Right.

DR. NORMAND: But then the exclusion criteria said you couldn't be hospitalized in 30 days prior to enrollment.

DR. BRISTOW: Right.

DR. NORMAND: So it's really within 11 months.

DR. BRISTOW: So the concept here is we want the previous heart failure hospitalization because that -- we know that that's associated with a higher event rate mortality and subsequent heart failure hospitalization, so that's the reason for that. But we didn't want unstable patients. We thought that would be a risk for device implantation.

DR. NORMAND: Okay. Now, I have a question about the randomization by center. At one point there's a number of 128 centers and then it goes down to 116 centers. The difference are centers that never recruited anybody?

DR. BRISTOW: Yes, let me get some help with that from someone, Dave or Fred or somebody, the 12 differential here. These are centers, I think, that did not finish in -- as active centers, but let me get confirmation of that. Sorry, with the slow kinetics here. This is a question we had not anticipated, as you can see.

DR. NORMAND: I might have a few more about the centers, so keep the binder open.

DR. BRISTOW: We'll keep working on that. Why don't we ask another question?

DR. NORMAND: Okay, the second question, unfortunately is related to the centers and that is, I believe in the FDA -- maybe the FDA can answer this one, though. The FDA indicated that several of the centers only randomized to one arm -- one of the treatment, either just pharmacy or medical therapy or not. I just want to understand why was that the case. Is it the case that the centers only had a accrued one person?

DR. BRISTOW: Yeah. Yes, in some -- yeah, I think generally very small numbers of patients and so the blocks that they had didn't allow enrollment in the two groups. They didn't get to those assignments.

DR. NORMAND: So it's 12 centers and four centers, 16 centers in total. I just want to make sure that indeed that's the reason. The numbers were so small and hence, they couldn't be randomized.