UNITED STATES OF AMERICA

DEPARTMENT OF HEALTH AND HUMAN SERVICES

FOOD AND DRUG ADMINISTRATION

MEDICAL DEVICE DISPUTE RESOLUTION PANEL

MEETING

	Friday, December 15, 2006

	The meeting came to order at 8:00 a.m. in the Grand Ballroom of the Hilton Washington DC North, 206 Perry Parkway, Gaithersburg, MD.  Scott Ramsey, MD, Chairman, presiding. 

PRESENT

SCOTT D. RAMSEY, MD, PHD, CHAIRMAN
JONATHAN D. SACKNER-BERNSTEIN, MD, FACC
	VOTING MEMBER
ALLEN A. HUGHES, PHD, CONSUMER REPRESENTATIVE
MELISSA WALKER, MS, RAC, INDUSTRY
	REPRESENTATIVE
DAVID DEMETS, PHD, CONSULTANT
WARREN K. LASKEY, MD, CONSULTANT
MICHAEL D. CRITTENDEN, MD, CONSULTANT
NANCY COLLAZO-BRAIER, PhD, EXECUTIVE SECRETARY
LES WEINSTEIN, ESQ, OMBUDSMAN

	

	A G E N D A

CALL TO ORDER 	3
	Scott Ramsey, M.D., Ph.D.
	Panel Chair

OPEN PUBLIC HEARING 	15

ACORN PRESENTATION 	23

BREAK 	99

FDA PRESENTATION 	101

LUNCH 	174

ACORN FOLLOW-UP/REBUTTAL 	175

FDA FOLLOW-UP/REBUTTAL 	192

OPEN PUBLIC HEARING 	203

OPEN COMMITTEE DISCUSSION 	213

BREAK 	268

FDA SUMMATION 	302

ACORN SUMMATION 	306

PANEL DELIBERATION AND VOTE 	319

ADJOURN 	345

	P R O C E E D I N G S
	(8:03 a.m.)
		DR. RAMSEY:  Well, good morning.  I'd like to call this meeting of the Medical Devices Dispute Resolution to order.  My name is Scott Ramsey, and I'm the Chairperson of the Medical Devices Dispute Resolution Panel.  I am an internist, and I'm a Professor of Medicine at the University of Washington in the Fred Hutchinson Cancer Research Center.  For those of you who haven't done so, please sign in with the attendance sheets that are out at the table just outside this room.
		I'd like to begin by asking the panel members to introduce themselves, and if you would, please, state your name and your area of expertise, position and affiliation, and I'll start with Dr. Laskey.
		DR. LASKEY:  Good morning.  I'm Warren Laskey, Chief of Cardiology at the University of New Mexico.
		DR. SACKNER-BERNSTEIN:  Jonathan Sackner-Bernstein, Chief Medical Officer of Clina Labs in New York, and a cardiologist.
		DR. DeMETS:  Dave DeMets, Biostatistician, University of Wisconsin.
		DR. CRITTENDEN:  Michael Crittenden, cardiac surgeon, VA Boston Healthcare System, Harvard Medical School, System Preventive Surgery.
		MS. WALKER:  Melissa Walker. I'm the Senior Vice President of Regulatory Quality and Compliance and Stereotaxis, and I'm the Industry Rep.
		DR. HUGHES:  Allen Hughes, George Mason University, School of Management, Assistant Professor of Decision Sciences and Information Systems, and I'm the Consumer Representative.
		DR. RAMSEY:  And I'll have the FDA Ombudsman  and Executive Secretary introduce themselves.
		MR. WEINSTEIN:  My name is Les Weinstein.  I'm the CDRH Ombudsman, and one of my roles is to facilitate the equitable resolution of disputes between offices in FDA Center for Devices in Radiological Health, and device sponsors, applicants, and manufacturers.  I convened today's Dispute Resolution Panel meeting at the request of Acorn Cardiovascular, Inc. to resolve a scientific dispute between Acorn and the Office of Device Evaluation. 
		I want to publicly thank the panel members for agreeing to participate in this important meeting, and to wish them well in their deliberations.  Thank you.
		DR. COLLAZO-BRAIER:  Good morning. I am Nancy Collazo-Braier, and I'm the Executive Secretary of the Medical Devices Dispute Resolution Panel.
		DR. RAMSEY:  Also, we have an FDA Press Contact here, Karen Reilly.  Are you available?  So she'll be available for questions.  If I could have everyone please silence your cell phones before we begin, that would be much appreciated.  
		I'm now going to read the summary of issues under dispute.  This meeting is being held at the request of Acorn Cardiovascular, Incorporated to resolve a scientific dispute between Acorn, the sponsor of pre-market approval application P040049, as amended, for the CorCap Cardiac Support Device, and the Office of Device Evaluation in FDA's Center for Devices and Radiological Health.  
		I will now proceed to read the Ombudsman's summary of the scientific issues in dispute for the Medical Devices Dispute Resolution Panel meeting of Acorn Cardiovascular, Inc.'s CorCAP CSD.  The letter begins as follows:
		"The CorCap cardiac support device manufactured by Acorn Cardiovascular, Incorporated, is a non-resorbable polyester mesh implanted around the heart to provide ventricular support, and reduce ventricular wall stress.  It is indicated for patients with dilated cardiomyopathy, who are worsening despite optimal medical management.  On August 12th, 2005, FDA issued Acorn a not-approvable letter regarding its pre-market approval application, P040049 for the CorCap CSD.
		Specifically, the FDA's letter said FDA believes that there is a lack of reasonable assurance of safety as described in 21 CFR 860.7(d).  In particular, FDA is concerned about the risk of perioperative death, safety of re-operation due to adhesions, and whether or not pericardial constriction will be observed in the long term in patients treated with the CorCap device.
		FDA believes that there is a lack of reasonable assurance of effectiveness as described in 21 CFR 860.7(e).  In particular, FDA is concerned about the amount of missing data for the primary endpoint, the lack of statistical significance in any secondary endpoints, and the absence of a specific patient population in which this device appears to be effective."
		In response to this decision, Acorn amended the PMA with a post hoc re-analysis of the original data set with the objective of identifying a sub-population in which CorCap CSD was safe and effective, referred to as the "focused cohort".  
		FDA issued a second non-approval determination on February 2nd, 2006 for the amended PMA.  The letter stated: "FDA believes the results of your focused cohort analysis have generated an interesting and promising hypothesis regarding a patient population in which your device may be safe and effective.  In order to demonstrate the safety and effectiveness of your device, we believe that the least burdensome approach is a prospective study that clinically validates the risk/benefit profile of your device in the patient population identified by the focused cohort analysis.  This study may be able to leverage the data from your early clinical studies."
		Acorn disagrees with the FDA's decision to issue the August 2005 not-approvable letter, as well as the subsequent February 2006 not-approvable letter, and the reasons for issuing them.  It is Acorn's opinion that the data submitted in the PMA, as amended, provides reasonable assurance of safety and effectiveness for the proposed intended use.  Specifically, Acorn believes the 300-patient clinical trial provides valid scientific evidence of safety and effectiveness, and that this result is not undermined by the concerns listed by the FDA in the August 12, 2005 not-approvable letter.  Thus, the Dispute Resolution Panel to whom Acorn has appealed the not-approvable decision, will be charged with reviewing and making a recommendation to the CDRH Center Director as to the approvability of the PMA; that is, does the PMA, as amended, provide valid scientific evidence that demonstrates a reasonable assurance of safety and effectiveness of the CorCap CSD for its intended use in the original patient population, and/or the focused cohort.  
		In consideration of that recommendation, the panel is asked to determine the following; whether the overall trial results for the primary effectiveness endpoint are interpretable and clinically meaningful.  Second, whether the secondary endpoint results are supportive of the safety and effectiveness of the device.  Third, whether FDA's safety concerns have been addressed by the data provided.  And, fourth, whether the data submitted by Acorn adequately addresses FDA's safety and effectiveness concerns for the original patient population and/or the focused cohort.
		This summary of scientific issues in dispute is an overview.  It is not intended to be a full and detailed statement of all such issues and arguments that will be presented at the panel meeting by FDA and the sponsor.  Specifically, FDA is to present data and analyses to support its not-approvable determinations, and Acorn is to present its reasons for disputing the not-approvable determinations.
		I'll now have Dr. Braier give an update of upcoming meetings and to deputize our temporary voting members for today's meeting.
		DR. COLLAZO-BRAIER:  Thank you.  I will now read into the read the deputization of temporary voting member statements and the conflict of interest statement.
		"Appointment to temporary voting status - pursuant to the authority granted under the Medical Devices Advisory Committee charter of the Center for Devices and Radiological Health dated October 27, 1990, and as amended August 18th, 2006, I appoint David L. DeMets as a voting member of the Medical Devices Dispute Resolution Panel for the duration of the meeting on December 15, 2006.  For the record, Dr. DeMets is a member of the Cardiovascular and Renal Drugs Advisory Committee of the Center for Drug Evaluation and Research.  He is a special government employee who has undergone the customary conflict of interest review, and have reviewed the material to be considered at this meeting."  This letter is signed by Randall Luther, Ph.D., Associate Commissioner for Policy and Planning, and is dated November 21st, 2006.
		"Appointment to Temporary Voting Status - pursuant to the authority granted under the Medical Devices Advisory of the Center for Devices and Radiological Health dated October 27th, 1990, and as amended August 18th, 1999, I appoint the following individuals as voting members of the Medical Devices Dispute Resolution Panel for this meeting on  December 15, 2006; Jonathan Sackner-Bernstein, M.D., Michael D. Crittenden, M.D., Warren K. Laskey, M.D., Scott D.  Ramsey, 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 letter is signed by Daniel G. Schultz, M.D., Director of the Center for Devices and Radiological Health, and is dated December 7, 2006.
		I will now proceed to read the conflict of interest disclosure statement.  "FDA Conflict of Interest Disclosure Statement - particular matter involving specific parties, Medical Devices Dispute Resolution Panel of the Medical Devices Advisory Committee, date of the meeting December 15, 2006.  The Food and Drug Administration is convening today's meeting of the Medical Devices Dispute Resolution Panel under the authority of the Federal Advisory Committee Act, FACA, of 1972.  With the exception of the Industry Representative, all members and consultants of the panel are special government employees, SGEs, or regular federal employees from other agencies, and are subject to federal conflict of interest laws and regulations."
		The following information on the status of this panel's compliance with the Federal Ethics and Conflict of Interest laws covered by, but not limited to, those found at 18 U.S.C. 2008, are being provided to participants in today's meeting and to the public.  FDA has determined that members and consultants of this panel are in compliance with Federal Ethics and Conflict of Interest laws.  Under 18 U.S.C. 2008, Congress has authorized FDA to grant waivers to special government employees who have financial conflict when it is determined that the Agency's need for a particular individual's services outweighs his or her potential financial conflict of interest.  Members and consultants of this panel who are special government employees have been screened for potential financial conflicts of interest of their own, as well as those imputed to them, including those of their employer, spouse, or minor child related to the discussions of today's meeting.  This interest may include investments, consulting, expert witness testimony, contracts, grants, gratis, teaching, speaking, writing, patent and royalties, and primary employment.
		Today's agenda involves a scientific dispute between the Agency and Acorn Corporation related to the approvability of a pre-market approval application for the CorCap cardiac support device.  The device is indicated for use in adult patients who have been diagnosed with dilated cardiomyopathy, and are symptomatic despite treatment with optimal heart failure medical management.
		Based on the agenda, and all financial interests reported by the panel members and consultants, no conflict of interest waivers have been issued in connection with this meeting.  Ms. Melissa Walker is serving as the Industry Representative, acting on behalf of all related industry, and is employed by Stereotaxis, Incorporated.  
		We would like to remind members and consultants that if the discussions involve any other products or firms not already on the agenda, for which an FDA participant has personal or imputed financial interest, the participants need to exclude themselves from such involvement, and their exclusion will be noted for the record. FDA encourages all other participants to advise the panel of any financial relationships that they may have with any firms of issue.  Thank you.
		I will also now proceed to read a few reminders.  Transcripts of today's meeting will be available from Neal Gross & Company, phone number (202) 234-4433.  Information on purchasing videos of today's meeting can be found on the table outside of the meeting room.
		Presenters to the panel in the two open public hearings today, if have not already done so, should provide FDA with a hard copy of their remarks, including overheads.  I will collect those from you at the podium.  I received three letters from people who were not able to make presentations during the public hearing.  I made copies of those letters available, and they are in the panel meeting packet with the panel members.  Thank you.
		DR. RAMSEY:  Okay.  We're going to proceed now with the open public hearing portion of the meeting.  It'll go from 8:15 to 8:45.  
		As we're getting started, if there's anyone here in the hotel who has chairs that can be brought in for the folks that are unfortunately standing in the back, I'll see if we can find some.  And maybe at the break, I'll see if we can open that wall in the back so there's a little more room for you.
		Okay.  A brief introductory 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 that it is important to understand the context of an individual's presentation.  For this reason, the 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 FDA, 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 this meeting.
		Likewise, the 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.  So during this public session, the speakers will be kept to 10 minutes, and just a procedural issue, I have a timer here, which you'll see up at the podium as you're speaking.  There'll be a one-minute warning, which you will see, and then at 30 seconds, I'll ask you to sum up, and forgive me for being rude, but I will have to have everyone stop at exactly 10 minutes, because we do have a pretty full agenda today.
		So our first speaker is Mercedes K.C. Dullum, M.D.  Press the button on the microphone there.
		DR. DULLUM:  Hi.  My name is Mercedes Dullum, I am a Staff Cardiac Surgeon at the Cleveland Clinic in Florida.  I was an investigator in the Acorn trial when I was at Washington Hospital Center, and currently have been allowed to participate in Acorn Continued Access Protocol, CAP program.  I have no financial interest in Acorn, and I am being compensated for my time and expenses.  I have no relationship with FDA, but I have served as a special government employee as a panel member in panel meetings previously.
		During the trial, our site, the Washington Hospital Center, enrolled many patients, and I was very impressed, and am very impressed with the results that occurred in my patients.  In fact, one of my patients felt so strongly about the benefit that he had received from the therapy and the placement of the device, that he actually spoke in the open forum at the original panel meeting.  He felt that he had gotten his life back by this treatment.  I have continued to see the patient, and follow with him, and he, indeed, is doing very well.
		I am here today solely as a treating physician having implanted approximately 10 of these devices, and to implore that the panel approve this so that we have this therapeutic option in our armamentarium for treating patients and caring for patients with heart failure.
		As we all know, there's a growing population of heart failure patients, and there are different etiologies for this, and that requires that we have different treatment strategies to treat these patients.  Based on my experience with this device, I feel that the cardiac support device is an important treatment that we should be allowed to treat our patients, and to use to help them.  As you know, it's a very devastating disease, and with cardiomyopathy, there aren't a lot of options.  They have been treated medically, and they just need another option to try to help them through.  And like I said, from my personal experience, I've seen this in the patients that I have treated and cared for.
		Thank you.  I appreciate the panel for allowing me the opportunity of speaking and presenting my viewpoint as a treating physician, and as a patient advocate.  That is my sole purpose here today.  Thank you.
		DR. RAMSEY:  Thank you, Dr. Dullum.  Excuse me.  Our next speaker is Dr. Robert D. Dowling.
		DR. DOWLING:  Good morning. I'd like to thank the panel for allowing us to give a few thoughts we have.  My name is Rob Dowling.  I am a heart surgeon, Professor of Surgery at the University of Louisville.  I'm Director of the Mechanical Circulatory Support Program, and Surgical Director of the Heart Transplant Program. I was an investigator in the Acorn trial, but I do not have any financial ties to the company.  I am being reimbursed for my travel expenses related to this meeting.  I have been fortunate in the past to both be present at and present to FDA panels. My remarks will be brief.  
		I first want to speak to the element need for new therapies for patients with heart failure.  We all see patients with advanced heart failure who have a poor quality of life, and yet aren't sick enough for heart transplantation or LVAD.  We have a gap in our armamentarium.  We all see these patients.  They're not doing well, but yet they're not sick enough for very advanced therapies.  Basically, what we do with these patients is we just see them more often in the clinic, and wait for them to progress to the point where they do need some other major operative intervention, again, such as heart failure or LVADs.
		Because of this gap between medical therapy, and LVADs and transplants, we were able to enroll 14 patients in the Acorn trial in our center.  I have been impressed with the results in our patients, and the results from the entire clinical trial.  I was most impressed with the improvements in quality of life that we were able to see in our cohorts of patients, and I think that is reflected in the data from the entire series.  The data I feel also shows some other very compelling findings regarding improvement in cardiac structure, particular LV size, LV shape, LV dimensions overall. I think all of these benefits are clinically meaningful for my patients.
		I was present at the first panel meeting.  As I mentioned, I have extensively reviewed the study data.  In my opinion, the benefits to this operative approach outweigh the risks.
		One final issue I would like to address is, I am aware of some concerns regarding re-operation in CorCap patients.  As I'm sure all clinicians know, almost all heart transplant patients have had previous operations.  At our institution in 2005, exactly two-thirds of our transplant recipients had LVADs in place.  This speaks to the fact that all transplant surgeons are skilled in re-operative techniques.  I have performed a transplant on a CorCap recipient, and I've talked to a number of surgeons who have also performed re-operative procedures on patients with CorCap devices in place.  Adhesions were present in my patients, and all the other patients, as is true of any patient who has had a prior operation.  In my experience, the adhesions were easily managed, and nowhere near the magnitude of adhesions that we see with LVAD recipients.
		Dr. Acker, at the last panel meeting, presented data from all the patients that had CorCap and underwent heart transplant, and clearly showed that there was no difference in any of the clinical outcomes in these patients.
		As a clinician, many of the issues regarding the physical analysis that had been discussed with the previous panel, and I'm sure will be discussed here today, are beyond my scope.  My hope today is that the panel, the sponsor, and the FDA can successfully address these issues, because we have a huge group of patients that need this therapy.
		I thank the panel members and all present for their time and attention.
		DR. RAMSEY:  Thank you Dr. Dowling.  Are there any other individuals who would wish to speak to the dispute panel?  If not, we will move on to Acorn's presentation.  		Before we start that presentation, I would like to remind public observers at this meeting that while the meeting is open for public observation, public attendees may not participate, except at the specific request of the panel.  So I believe our first speaker is Dr. Karen Becker.  Yes?
		DR. BECKER:  Yes.
		DR. RAMSEY:  Okay.  You have the floor.
		DR. BECKER:  Thank you.  Good morning, ladies and gentlemen.  My name is Karen Becker, and I'm representing the sponsor, Acorn Cardiovascular in this proceeding today.  I want to express appreciation to both FDA and the panel for providing this forum to consider the approvability of the CorCap CSD PMA.  
		This is the agenda that Acorn is going to proceed with this morning.  After some brief opening remarks, Dr. Mariell Jessup will summarize the clinical data in the PMA, followed by expert comment on the scientific issues in dispute.  The expert comment is divided into three specialties.  We have Dr. Steve Piantadosi and Dr. Don Rubin speaking about statistical and trial methodology issues, Dr. Randall Starling and Dr. Doug Mann as cardiologist, and Dr. Steven Bolling and Michael Acker as cardiothoracic surgeons.
		Just to provide a brief context for the proceeding, I want to note that the nature of this dispute resolution process is not typical of the Advisory Panel process that you may have participated in in the past.  As I'm sure you know, and have been briefed by the Ombudsman, the Food, Drug and Cosmetic Act, as amended in 1997, included a provision for a process to resolve scientific controversies between the sponsor and the agency.  CDRH established this panel to do that, and one of the requirements for bringing a matter to this panel is that there are sound scientific grounds that support an appeal; and, also, that the matter is sufficiently complex to warrant specialized experts and an independent review.
		So, as you know, the CorCap CSD is a non-resorbable polyester mesh implanted around the heart to provide ventricular support, and reduce ventricular wall stress.  It's indicated for patients with dilated cardiomyopathy who are worsening, despite optimal medical management.
		Today we will be speaking in great detail about the pivotal trial of the CorCap CSD, but we want to be sure to point out that there is considerable science underlying the design of this technology.  That includes laboratory studies, and proof of concept studies, and animal models of heart failure, dog, bovine, and sheep models.  All of this data is in your panel pack, and should you have any questions about this, experts in this area are available to you to discuss this information.  This is obviously important because it provides additional weight of the evidence in your deliberations.
		Just a brief note about the history, the CorCap clinical trial was started in 1999, seven years ago, the PMA submitted in 2004.  The Circulatory Systems Devices Panel considered the approvability of the PMA.  Four panel members voted for approval, nine panel members voted against approval.  The principal concerns at that panel meeting were missing data, interpretation, and clinical relevance of the primary endpoint, and some safety questions.
		FDA, following that, issued a not-approvable letter.  Acorn amended the PMA with additional information.  FDA still felt that their concerns had not been addressed, and issued a second not-approvable letter.  That is the administrative action being appealed, and in June, 2006, their request for referral to this panel was granted.
		It's important for you to recognize, we think, that there's more information available to you today than was available to this Circulatory Systems Devices Panel.  They did not review the amended PMA, or additional information that you've been provided with.  The amended PMA provides data on potential investigator bias regarding major cardiac procedures, that was one important issue and concern raised regarding the trial design.  The amended PMA also provided supplemental information on safety at re-operation, extended follow-up on mortality, a post-marketing study designed for safety and long-term outcomes, a post hoc analysis of patients most likely to benefit from the procedure, and a revised indication for use based on ventricular size.
		Additionally, you have more information on the imputation methodology that was used for COR assessed NYHA, and also, you have an independent validation of that imputation, as well as a blinded validation of that methodology for handling missing data in this trial.  And, finally, submitted in your panel packs is written testimony from well-qualified experts who reviewed all the data, and you will be hearing from them today.
		I have three corrections to the record, or clarifications to the record, that we would like to just put out here for you.  The first is that just to be clear, the protocol for the CorCap pivotal trial always specified an ITT analysis for the primary endpoint.  FDA did require a change to the analysis plan at the end of the study, because they were concerned that the imputation methodology proposed by Acorn would not be sufficiently robust, and they recommended multiple imputation, which we agree was a very good recommendation, and that was accepted by Acorn.  And the analysis plan using that methodology was developed by blinded statistician.
		The second point is that we understand that there's some concern that the unblinding of the clinical trial may have created some bias in this analysis plan.  We want to just clarify that that would not have been possible.  When FDA concluded that  Acorn's initial imputation method would not be acceptable, and recommended multiple imputation.  Acorn first requested more information about that, never having heard of multiple imputation.
		In June of 2004, Acorn officers were unblinded, but no one in the Regulatory Affairs Department or the staff responsible for making decisions about the analysis plan, including the statisticians, were unblinded.  In August of 2006, Acorn agreed to impute NYHA data using multiple imputation.  FDA acknowledged receipt of that decision.  It was only after that decision was made that the study was unblinded to the Regulatory Affairs Director and to the Manager.
		So, in conclusion, we have more information about this issue if you would like, but there was no opportunity for unblinding to have an impact on the design of the analysis plan.  And, further, as you'll hear later this afternoon, the multiple imputation methodology has been validated by an unblinded scientist.
		The third point was just to clarify that the reason that there was missing data in this trial is that in the course of the study, discussions between the sponsor and FDA resulted in a request by FDA to include a blinded assessment of NYHA, rather than site assessment, and so Acorn developed a method to do that, and validated that study.  And that validation has been published, and we have more information about that, should you wish to hear it today.
		Finally, this slide just shows you a brief statement of the data that we feel provides reasonable evidence of safety and effectiveness for this device, and you'll be hearing more about that in detail.  This was a well-controlled study, executed with a high degree of compliance to the study protocol.  Mortality and adverse events were similar between groups, and in terms of effectiveness, the success criteria for the  trial was met in terms of the primary endpoint.  Secondary endpoints were supportive, and in addition, pre-clinical studies, a small safety trial provide additional evidence in support of effectiveness.
		Finally, the statistical methods applied to this trial are sound and have been validated, and the sponsor has submitted a proposal to the FDA for a 500-patient post-approval study.  
		So, in conclusion, the scientific issues in dispute that you will be deliberating on, in our opinion, having evaluated this data carefully, the data demonstrate that the primary endpoint result is clinically relevant and beneficial, the statistical analysis of the primary endpoint is reliable, the secondary endpoint results do support the study hypothesis, the safety profile is reasonable in consideration of the benefit, and the original patient population adequately addresses safety and effectiveness questions posed by FDA.  The focused cohort analysis is post hoc, and not necessary for an approval determination.
		Now I'd like to turn this over to Dr. Mariell Jessup to give you a summary of the clinical trial.
		DR. JESSUP:  Good morning.  My name is Mariell Jessup, and I'm a Professor of Medicine and Medical Director of the Heart Failure and Transplant program at the University of Pennsylvania.  I have no financial interest in the company, and I am being compensated for my time.  I was a member of the CorCap CSD pivotal trial Steering Committee, and will now briefly present the design and results of that study.
		The CorCap CSD trial was a 300-patient prospective randomized controlled multi-center trial.  Patients were accrued as two separate groups with and without the need for mitral valve repair or replacement, which most of the slides will depict as MVR.  There were 29 slides in the U.S. and Canada.  Patients were randomized to treatment, either the CorCap CSD implant, or controlled, which was to continue on medical therapy.  In both the MVR and the non-MVR groups, it's important to emphasize that all patients were on optimal medical therapy for at least three months prior to randomization, and continued that therapy for the duration of the trial.
		The trial was designed according to an intention to treat analysis powered for 300 patients.  The data analysis plan pre-specified pooling of both  strata, and reporting as one cohort.  And we felt that this was justified, because the inclusion criteria in both strata were virtually identical, and the endpoints for both strata were identical.  Patient functional status was evaluated at three, six, twelve, and every six months until the common closing date of July 4th, 2004.
		This slide summarizes some of the major inclusion and exclusion criteria for the trial.  We enrolled men and women aged 18 to 80 years.  They could be New York Heart Association Functional Class 3 or 4 heart failure of ischemic, or non-ischemic etiology.  They had to have had a left ventricular ejection fraction of less than 35 percent, and a large left ventricle, with the left ventricular and diastolic dimension of greater than 60 millimeters.  
		The exclusion criteria are shown below.  The patients could not have had a CABG prior to this surgery, nor could they have been on an active transplant list, so I want so summarize that these patients continued to be symptomatic with a poor exercise tolerance as measured by 6-minute walk test, had a low ejection fraction, and enlarged hearts, and were symptomatic, but stable.
		This slide shows the primary endpoint of the trial.  The clinical composite comprised of three components, mortality, which was used as a safety outcome, and two efficacy components, major cardiac procedures, and NYHA class.  The primary endpoint was not intended to be broken down into its components, but rather to construct a composite that would make sense biologically, and be coherent with a natural history of heart failure; that is, to get a clinical picture of the disease.  Thus, the study was not designed or powered to separate the three components.  Each component, however, was clinically relevant and was detectible by the patient.
		The three components that comprised the worsening category could account for every clinical outcome for a patient with heart failure.  For example, patients who were considered worsened could either have died during the study, could have had a major cardiac procedure that was adjudicated by a blinded committee as being caused by worsening heart failure, or could have had worsening NYHA functional class as assessed by a blinded New York Heart Association assessor.
		Importantly, if patients were to be considered improved, they had to have had a decrease in New York Heart Association Functional Class by one or more class, as assessed by a blinded assessor, and they couldn't have had anything that could have categorized them as worsening during the trial.
		This slide depicts patient enrollment.  There were 300 patients who were stratified either to the mitral surgery stratum, reminding you that patients in whom the site investigators determined that mitral surgery was required, or the no-mitral surgery stratum, and randomized in a permuted block design for each stratum to treatment or control.  All patients, as I've said, were maintained on optimal medical management.
		There were 148 patients in the CorCap or treatment group, 91 who received mitral valve repair or replacement, plus the CorCap cardiac support device, and 57 who received CorCap alone.  There were 152 patients in the control group, 102 who received mitral valve surgery, and 50 were continued on optimal medical therapy alone.
		It's important to emphasize that the CorCap CSD pivotal study was a well-conducted study.  It was rigorously designed, conducted in accord with the study protocol, and had a high degree of follow-up and compliance, as you will see in the next several slides.  While the study was designed to reflect a minimum of 12 months of patient follow-up, we actually had a 23-month median follow-up on the common closing date of the study of July 4th, 2004.  This 23-month follow-up directly relates to the primary composite endpoint; that is, the primary endpoint was calculated based not just on 12 month data, but included all data available at the common closing date.
		Of note, vital status was collected on that date for all but one of the 300 patients enrolled.  The patient was followed up through the 12th month visit, and was last known alive 19 months after the initial surgery.  
		This slide shows patient compliance for specific measures at six months and twelve months.  You can see, for example, test completion for blinded assessment of the New York Heart Association Functional Class was 87 percent at six months, and 95 percent at twelve months.  We had 96 percent compliance with echo measurements, and 97 percent compliance with the Minnesota Living with Heart Failure Questionnaire at twelve months.  In some instances, there was missing data, because patients were too sick to exercise, but overall attendance at all visits was quite good.
		This table depicts the intention to treat primary composite endpoint result.  As indicated, patients were placed into three categories, improved, same, or worsened.  In this trial, the treatment group had more patients improve, and fewer patients worsen than in the control group, with a median of 23 months of follow-up.  The proportional odds ratio was 1.73, indicating that the treatment patients with the CSD compared to control had a 73 percent greater odds of being in a better outcome category.  This was statistically significant at a P value of 0.024.  Thus, the primary objective of this trial was met.
		As discussed previously, the three components in this trial accounted for every clinical outcome for each patient, and demonstrated that CorCap patients had a better clinical outcome than control patients.
		As noted, the study was not designed or powered to evaluate each stratum individually, but the results by strata for the primary endpoint are worth noting, and are depicted on this slide.  As you can see, both strata favored the CorCap group.  The directionality and magnitude of the effects are similar between groups, as reflected in the odds ratio and confidence intervals.
		Now I've mentioned that the study was not designed nor powered to separate the components of the primary endpoint, but the clinicians in us find it useful to look at each component individually to see how they trended.  Let's first look at major cardiac procedures.  At every point in the trial, the treatment arm had fewer major cardiac procedures than the control arm.  The difference was, in fact, statistically significant at a level of 0.01.  
		This table shows the major cardiac procedures indicative of worsening heart failure included in the trial. It's important to remember that some patients had more than one event.  As can be seen, the number of patients experiencing events in the treatment arm was less than in the control arm.  Treatment patients had fewer major cardiac procedures, specifically, a marked reduction in the need for cardiac transplantation, and/or a ventricular assist device.
		In addition, there were fewer repeat mitral valve surgeries, and fewer bi-ventricular pacers implanted.  Although it's not displayed here, an analysis of the results, excluding bi-ventricular pacing, showed no affect on the overall outcome; that is, results still significantly favored the CorCap, even when omitting patients who received bi-ventricular pacing.
		As the second component of the composite, this table shows the change in Core lab NYHA classification.  This is based on a per-protocol analysis excluding subjects who died, or experienced a major cardiac procedure, in order to evaluate only the change in New York Heart Association Functional Class.  The table summarizes the Core lab NYHA classification from baseline to the last follow-up visit.  
		As discussed previously, patients were only considered improved if the NYHA classification improved by one or more full classification, and worsened if NYHA deteriorated by one or more class.  A greater percentage of patients in the CorCap group improved, compared to the control.
		This intention to treat analysis was conducted to recover NYHA data that was missing due to patient death, or to patients undergoing MCPs.  Specifically, we counted patients who had VADs, transplants, and other major cardiac procedures that were adjudicated as worsening heart failure, as one class worse than baseline NYHA, and those that died as Class 5 NYHA.  The results show more treatment patients improving, and fewer treatment patients worsening with respect to NYHA functional classification, with a proportional odds ratio of 1.73, identical to the odds ratio for the primary endpoint of the trial.
		This slide shows the third component of the  primary endpoint, mortality, for the entire 300-patient cohort as presented in the original PMA.  This analysis shows that mortality was similar between the control and the treatment arms.  There was, likewise, no difference in the mode of death between groups.
		I'd like to turn to the safety outcomes.  This table details the number of patients experiencing serious adverse events by treatment group throughout the duration of study follow-up by the common closing date.  Overall, 78 percent of patients in the control group, and 81 percent of patients in the treatment group, had a serious adverse event.  The number of patients and the type of adverse events experienced were not statistically different between the treatment and control groups.  No device-related adverse events occurred during the study.  Also, there were no adverse events or complaints reported related to sizing or fitting of the CorCap CSD, and no adverse events related to cardiac constriction.  
		The sponsor performed an update of mortality and serious adverse events in April of 2005.  This table presents the serious adverse events results.  Overall, 83 percent of patients in the treatment group, and 79 percent of patients in the control group experienced a serious adverse event.  There was a higher percent of patients experiencing hemodynamic or renal compromise in the CorCap treatment group.  Note, that analysis of hemodynamic compromise by Cox regression showed that early events, only early events within 30 days after surgery in the no-MVR stratum were significantly different.  I would remind you that the no-MVR meant that the control group was not undergoing surgery.  As with the July 2004 analysis, there were no adverse events or complaints reported related to sizing or fitting of the CorCap CSD, and no adverse events related to cardiac constriction.
		Here we see mortality depicted as a time period analysis for the purpose of safety analysis.  Note that one of the deaths in the no-MVR CorCap group occurred before the planned surgery to place the device.  Although, the perioperative risk in the CorCap in the no-MVR stratum is elevated compared to controls who did not receive surgery, it should be noted that by 12 months, the likelihood of death was similar across study groups.  Drs. Acker and Bolling will comment on the issue of perioperative mortality later in the presentation.
		This slide shows mortality as of the safety update conducted on April 15th, 2005.  During the additional follow-up, there were no differences observed between groups with regard to mortality.
		This slides shows the structural functional laboratory and clinical secondary endpoints.  The treatment difference for left ventricular end- diastolic volume, LVEDV, and left ventricular ejection fraction favored CorCap.  Both the control and treatment groups demonstrate a reduction in end-systolic volume, indicating a decrease in left ventricular size.  The average reduction in end-systolic volume over the 18th month follow-up period was greater in the treatment, compared to the control group, with an overall treatment difference of 15.2 milliliters.  
		Like left ventricular end-diastolic volume, left ventricular end-systolic volume decreased progressively over the follow-up period, rather than abruptly after surgery.  This is in contrast to surgical procedures where parts of the heart are removed, such as SAVER or the DOR procedure, where the heart immediately is shrunken after surgery.
		Cardiac sphericity index is calculated as the ratio of left ventricular length to left ventricular width, both measured in diastole.  A normal cardiac sphericity index is approximately 1.58.  As the heart enlarges and changes shape from an American football to a soccer ball, the length-width ratio approaches one which is a perfect sphere.  Therefore, any intervention which increases the length to width cardiac sphericity index to greater than one would be returning the heart to a more normal shape.  There was an increase in sphericity index for both groups, indicating a beneficial change in shape.  There was, however, a larger increase in sphericity index for the treatment group, approximately 0.042.  
		The change in shape is likely related to a design feature of the CorCap CSD, in which the compliance or stretchiness is greater in the longitudinal, the base to apex direction, as compared to the transverse, or circumferential direction.  Not only is the heart smaller, but has a more normal shape, which provides mechanical and bio-energetic advantages.  Note the results for mass, left ventricular end-diastolic dimension, and left ventricular end-systolic dimension, LVEDD and LVESD, were also trending in favor of the CorCap.
		Turning to the functional response to this device, both the control and treatment groups demonstrate a reduction in Minnesota Living with Heart Failure score.  A lower score translates to a better quality of life.  The treatment group, however, had a greater reduction with an average difference of 4.47 units.  The improvements in clinical score were evident at three months, and were sustained over 24 months.  
		In the physical function domain of the SF-36, a higher score indicates a better quality of life.  The treatment patients had a greater score with a treatment difference of 5.41, indicating a better quality of life in the physical function domain, compared to control patients.  Again, the improvements were evident at three months, and were sustained over 24 months.
		As you can see, the majority of secondary endpoints favor the CorCap group, providing support to the primary and significant composite endpoint results.  These are individual P values, the adjustments and interpretation of which will be discussed later by Dr. Steve Piantadosi.
		So, in conclusion, the CorCap randomized trial achieved its primary endpoint.  Secondary endpoints, including left ventricular end-diastolic volume, left ventricular end-systolic volume, sphericity, Minnesota Living with Heart Failure Questionnaire, and the SF-36 provide support to the primary endpoint.  The device demonstrated an acceptable safety profile, and we therefore conclude that the data submitted provide reasonable assurance of safety and efficacy. 
		Thank you.  I'd like to introduce Dr.  Steven Piantadosi.
		DR. PIANTADOSI:  Thank you, Dr. Jessup.  My name is Steven Piantadosi.  I will be the moderator for the expert panel portion of the sponsor's presentation.  I'm a clinical trials medical -- 
		MR. WEINSTEIN:  Excuse me one minute, please.  What do you mean by "expert panel"?  This is the only panel that is here today, so the sponsor's experts can be called the sponsor's experts.
		DR. PIANTADOSI:  I'm sorry.
		MR. WEINSTEIN:  But they do not constitute a panel.
		DR. PIANTADOSI:  The sponsor's expert.  Please forgive me for misspeaking.
		I am a clinical trials methodologist and Director of Biostatistics at Johns Hopkins Oncology Center, and I'm Professor of Oncology, Biostatistics, and Epidemiology at the Johns Hopkins Medical Institutions.  I have no vested interest in the sponsor.  I am being paid for my time here as a consultant to the sponsor.
		This slide shows the list of sponsor experts who will present to you today, and I'll let each of them introduce themselves when they come to the podium.  Some of these individuals were investigators on the trial, and can speak to details of the trial design and conduct.  Others are clinical experts, or data analysts and clinical trials experts.  The details of their academic affiliations are provided in the written materials.
		I'd like to sketch briefly the methodology of our review on behalf of the sponsor.  Each consultant independently reviewed all of the relevant data, including the items listed under the first bullet, the PMA, as amended in December 2005, relevant published literature, proceedings from the FDA Advisory Panel meeting, the not-approvable letters from August 2005 and February 2006, as well as the study protocol.  The consultants met, they discussed these matters, and jointly provided a consensus opinion, which you have in your panel pack.  In addition, written consensus opinion has been provided to you in the form of the expert memorandum dated November 2006.
		A brief sketch of some of the reasons why there is contention, and why we're here discussing these matters today.  This slide lists some of the pitfalls that the consultants have attempted very assiduously to avoid, and they are; first, an overly strict adherence to P values as a measure of evidence.  And I'll be discussing this later, particularly in the context of the secondary outcomes.
		Taking subgroup findings as primary and definitive, this will also be discussed later.  You've heard a little bit about it already from Dr. Jessup regarding the clinical outcomes.  Deconstruction of the primary outcome, also a pitfall - the study was never designed or intended for this.  Misunderstanding of the role of stratification in this multi-center trial, we'll return later to talk about that.  And, also, misinterpretation of the potential effects of missing data.  You will see steps taken by the sponsor and consultants to avoid these pitfalls, because they can lead to incorrect conclusions.
		The conclusions that we'll lend support to shortly include the following; the primary endpoint is clinically meaningful.  There is a small amount of missing information, as distinguished from missing data, and it does not compromise the result.  There is no evidence that bias has affected the primary endpoint.  The analysis of that endpoint is in accord with proper statistical methods, and as specified in the study protocol.  The results in the two strata are clinically relevant.  The results for the secondary endpoints are supportive of the primary finding, and the product has a reasonable safety profile, and the benefits outweigh the risks.
		To support each of these conclusions, we're going to discuss four principal areas, after I give a brief overview, the primary and secondary endpoints, safety, and benefit/risk, and we'll wrap up with some conclusions regarding the issues under discussion today.
		With regard to the overview of the study, you've heard that this trial is a well-designed and well-executed study.  It's a largely successful implementation of a logistically complex trial.  Trials, by their very nature, are messy experiments, and this one is no different.  The surgical nature of the trial virtually precluded the use of blinding; but, nevertheless, there were additional techniques applied to reduce bias, including the blinded Core lab, echo, and so on, the CERC, the data monitoring process, and the fact that the sponsor and investigators were masked to the aggregate results.
		You've heard details regarding the primary endpoint being an appropriate composite.  The study was stratified to remove an extraneous source of variation, which I'll return to in a moment, and the secondary outcomes, in addition to the primary, were protocol specified.
		I'm going to begin this commentary on primary endpoint by discussing just a couple of points from a methodologic perspective.  The primary, as you heard, is a composite of three clinical outcomes that were selected to assess in a coherent way the progression of the disease.  Each patient is classified as improved, the same, or worsened, and the important principle here is that no subject on the trial could escape a valid classification for their disease status following therapy.  
		The study was designed and powered for the composite.  The clinical benefits and changes, however, being in the same direction within each component is important.  Mortality is viewed primarily as a safety endpoint.  It enters into the algorithm for the primary outcome, because individuals had to be alive to be classified as the same, or improved.  And the study was never designed or powered to deconstruct that primary.
		There is a modest concordance between the site-assessed and COR NYHA; however, it's not a serious problem, as we'll see shortly.  And there is a small amount of missing information for the composite, making multiple imputation appropriate.  And I'm going to call on Dr. Donald Rubin to explain the difference between missing information, missing data, and to describe the details of the multiple imputation procedure.
		DR. RUBIN:  Thank you, Dr. Piantadosi.  I'm Donald Rubin.  I'm Professor of Statistics at Harvard University.  I have no financial interest in Acorn.  I am being compensated for my time and expenses here.
		As was just stated, there is a small amount of information for the composite endpoint, the primary endpoint, and multiple imputation is entirely appropriate to handle this problem.  The reason missing information arose in the composite primary endpoint is that one component of it was the change in lab assessed NYHA from baseline.  And this was an administrative decision that was made.  In the early part of the trial, only site-assessed NYHA was recorded, so baseline lab assessed NYHA was only recorded in the latter part of the trial for the final 126 patients. And data was missing by design for the first 174, so that sounds like a lot of missing data, and there is a lot of missing data, but there's very little missing information for the primary endpoint.  There's a distinction that I'll address in greater detail later, but the amount of missing information for the primary endpoint is something well less than 10 percent, closer to 2 percent, as a matter of fact.
		Baseline site-assessed NYHA was recorded for all 300 patients.  FDA appropriately suggested handling the missing data NYHA by multiple imputation, which will be abbreviated MI in the rest of these slides.  It's important to realize that if you're going to apply intention to treat analysis, which I strongly advocate, you have to do imputation of missing data when you do have it in a primary endpoint.  And you can do that either explicitly by imputation, or you can do it implicitly using models. I much prefer doing it explicitly, so you can see exactly what you're doing.
		Now it's important to realize that multiple imputation is very different from single imputation methods that are ad hoc; for example, last observation carried forward, or filling in the mean, or case deletion.  It's completely different.  It's well-established as a valid method of dealing with missing data, as long as a realistic model is used.  With multiple imputation, each missing data is replaced by multiple values, and these multiple values are used to reflect the uncertainty about the correct value to impute.  So as you'll see very shortly, you don't put in the best prediction, you put in values that represent reasonable predictions, and the uncertainty about the value to impute.  These multiple values create repeated data sets, repeated complete data sets, and each completed data set is analyzed within standard complete data methods, so that allows you to use the standard software to analyze data sets that have missing values.
		I proposed this multiple imputation in the mid-70s, and it's had a very large number of evaluations supporting its validity and robustness to modeling assumptions.  These evaluations are theoretical.  By analysis, they're based on simulated data, they're based on real applications in many examples going back to the early examples that the United States Census Bureau, the National Center for Health Statistics, and many applications.  And, in fact, there's a current application at CDC that I'll briefly talk about later.
		Now standard multiple imputation assumes ignorable missingness, and "ignorable" is in quotes there, because it's ignorable in a particular technical sense.  And, in fact, because of this technical definition, that is one of the reasons why the initial panel - they didn't understand this technical definition, and there was some confusion about that, so I'll address what this technical definition really means, as well.
		Now this is an illustrative example of multiple imputations.  Oops, how do I get this to go  in parts?  This is supposed to be in three different slides, and it's not doing it, so this is much too busy.  Okay.  Back one more.  No - well, the first box below there is not supposed to be there.
		So this is a depiction of an example that has X fully observed, and Y partially missing.  The blue dots are the observed values where they're both X and Y observed.  The vertical dotted lines represent values of X that are observed, but there's no Y, so this represents a particularly simple example where there are observed values that are the blue dots, and there are some units that have X observed, but you don't know the value of Y, so when you impute Y, it's going to be somewhere along this line, somewhere along this line, somewhere along that line.
		Now if you imputed the best value in some predictive sense, you impute it right on the regression line, so this line is based on the observed data that relates Y to X.  It's the least squares line or fit of Y as predicted from X.  
		Now with multiple imputation, what you do is you don't put them right on the regression line.  You look at this regression line, its predicted values, but you look at the deviations of the observed data from that line, and you impute values that are reasonable given what you've observed.  So, for example - boy, this isn't working right at all - the triangles are the first imputed value, so the - can we get this right or not?  We can't.  Okay.  I'll have to talk to it incorrectly. 
		The triangles, the orange triangles are the first imputed value of missing data.  So if you look at the blue dots in combination with the triangles, you now have one complete data set.  And that complete data set is analyzed using standard complete data methods.  And you'll notice that in this depiction, the triangles have about the same amount of deviation from this line as the observed data do.  
		The second imputed data set is another random draw from this observed data, and they're just on and off the line, as well, with about the same kind of deviations.  So the blue dots, plus the triangles, create the first imputed data set, and the blue dots plus the diamonds create the second imputed data set.  Each of these imputed data sets is analyzed using standard complete data methods, because the resulting data set looks just like a complete data set.  And you can do this repeatedly.  And what you do is you will find out that the variability between the answers across the multiply imputed data sets, as completed by multiple imputation, reveals the uncertainty that's due to the missing data.  And the average of these answers gives you the right answer.  And there have been dozens and dozens of applications of this.  In fact, I recently Googled multiple imputation, and found over 600,000 hits, so in the last two decades become very, very popular; and, in fact, roughly five to ten years ago, SAS included it in its software because users demanded it as a way of handling missing data.  It's very intuitive.  You can see what you're imputing, and it works extremely well.
		What "ignorable" means here, and I'll just make this one comment.  I'll go back to it in a moment, is that "ignorable" missing just means that the values to multiply impute can be predicted in this random way from the observed data.  If it's non-ignorable, it means the value to impute for this missing value is systematically off the regression line.  Maybe it's way up here, maybe it's way down there.  If it's non-ignorable, it means that it's missing because of its numerical value; and, therefore, unpredictable from the observed data.  All ignorable means is that it's basically the missing data are predictable from the observed data.
		Now in the Acorn's PMA, they use the Multiple imputation model following the suggestion of FDA.  It was developed in collaboration with the local outside expert, not me, and implemented using SAS Version 8.2 PROC MI and PROC MI Analyze.  And in this model, it assumed ignorable missingness, which I'll say more about, is entirely appropriate.  It assumed a normally distributed NYHA, which is arguably not appropriate because, as we've seen, NYHA is ordinal four levels.  And it only included some baseline predictors with the multiple imputation model.  Using this model, nevertheless, the analysis of the primary endpoint after multiple imputation favored CorCap over control with a P value of .024, and an odds ratio of 1.73, and those are the results that you've seen before, because those are the results that are in the PMA.
		There is a lot of evidence, by the way, that you can have lots of different models that would give the same results following multiple imputation because these hundreds of publications that I referred to really indicate it's terribly robust, especially with a modest amount of missing information.
		Now the criticisms of the PMA multiple imputation model that were voiced in the panel meeting of June `05 were three, basically.  One, the missingness was not ignorable because the fraction of missing values, the baseline NYHA was too high.  The second criticism is there are too few predictors included and possibly improperly selected because there was some stepwise selection of them that was used.  And three, the missing NYHA was not normally distributed but ordinal.
		The first criticism, Criticism One, represents a misunderstanding of the technical definition of non-ignorable.  And by construction, and I'll show you later, by construction the missingness is, in fact, ignorable, for comparison to CorCap and control.  Criticisms Two and Three do deserve consideration, however, and they are addressed, they have been addressed.
		First I wanted to discuss the difference between fraction of missing data versus fraction of missing information, which is a key point of confusion often.  This is an artificial example just to emphasize this.  Let's suppose you have 1,000 patients where the primary endpoint is changing weight from baseline in pounds.  Now in the first 500 patients, you only measure weight in kilograms.  In the second 500 patients, you measure weight in pounds and kilograms.  Well, the fraction of missing data on weight in pounds is 50 percent.  There's no doubt about that, so half the data, in some sense, on the primary endpoint is missing.  But the fraction of missing information on the primary endpoint is tiny, because weight in pounds is so highly correlated with weight in kilograms.  Roughly 2.2 pounds equals a kilogram, so it's only the rounding error in that.  
		The point is that because weight in pounds and weight in kilograms is so highly correlated, the fraction of missing information on something involving weight in pounds is tiny, even though the fraction of missing data on weight in pounds may be high.  In our application with Acorn, the correlation with lab-assessed NYHA is based on many predictors, other than site-assessed NYHA, so we're not just relying on site- assessed NYHA to do the prediction of lab-assessed NYHA when it's missing, but we're using many variables to do this prediction.  For example, severity index, ejection fraction; in fact, in some of the models there are dozens and dozens of variables being used to do this prediction, not just one.  And that's how we get fractions of missing information about the primary endpoint well below 10 percent.
		Now I want to address this misunderstanding of ignorable versus non-ignorable missing data.  Now first, neither the fraction of missing data, nor the fraction of missing information has anything to do with the technical definition of ignorability of missing data, so that's just a misunderstanding from the original panel.
		Non-ignorable basically means it's missing, a value is missing because of its numerical value.  In that depiction, that artificial example, it basically means that the value that's missing is somewhere off the regression line, off the prediction line, unrelated to the observed data, whatsoever.  So if it's non-ignorable, the value to impute is unpredicted from the observed data.  It's systematically off the prediction line, and you have no idea where to put it.  It could be high, could be low, you just don't know.  So in that case, you sort of - what can you do?  And in our example, it is ignorable for the following reason.
		In our example, in the Acorn case, lab-assessed NYHA was missing because of an administrative decision, not because of its numerical value.  It had nothing to do with its numerical value.  Early versus late enrollment in the trial was the reason why lab-assessed NYHA was missing.  And because the Acorn trial was blocked in time, and randomized to CorCap or control, there is no way the missingness is anything but ignorable for comparing CorCap and control.  It is ignorable by definition for comparing CorCap and control.
		Now to address the other two criticisms, we decided to investigate the sensitivity of the resultant primary endpoint analysis to different versions of imputation models that address the non-normality of NYHA, the non-normally distributed NYHA, and the predictor choices.  There were three more SAS-based multiple imputation models that were applied.  These use updated Version 9.1 of SAS, because this updated version allowed an ordinal variable; whereas, the earlier version of SAS did not, and we were stuck with normal.  So this updated version of SAS allowed more flexible and realistic multiple imputation models.  So all three of these models assumed an ordinal NYHA, and used 100 multiple imputations, that's 100 imputations of the values on and off the regression line, or on and off the prediction line.  And there's really no reason to use 100 examples like this.  There's a lot of evidence that three to five imputations is fine, but there's no reason not to use more.  It just makes it more efficient.  So the first model used more predictors, some post baseline, which is perfectly valid and usually more efficient.
		Using this SAS-based model, the P value for the primary endpoint was .029, the odds ratio 1.69, essentially the same answer as with the PMA multiple imputation model.   The second SAS-based model used more predictors, but no predictors post baseline, and the P for the primary endpoint now is .033, with an odds ratio of 1.67.  Again, results that are significant, and odds ratio that's essentially the same as in the PMA.
		The third SAS-based model was like model one, that's more predictors post baseline, but used distinct models for the two randomized groups.  That's using one model for the CorCap group, one model for the control group, which is what I prefer, to avoid cross-contamination of the imputation models from one treatment arm to the other.  Now we got a P for the primary endpoint of .021, with odds ratio of 1.79, so all three of these additional SAS-based models, which is based on more realistic assumptions, supported the PMA results completely.
		Nevertheless, I proposed using a final multiple imputation model that uses special state-of-the-art method developed for CDC for Anthrax vaccine trials.  I've been working on this for about three or four years.  It extends methods in a publication that I have in 2003, which is a big multiple imputation projects for National Medical Expenditure Survey at the National Center for Health Statistics.  And it's used to address missing -- this model is used to address data.  And the Anthrax vaccine trial is much more challenging application, but the good thing about this model is I regard it's completely state-of-the-art, and it allows any kind of variable you can imagine, allows all sorts of complex relationships, and we applied it to the Acorn data in the following way.
		NYHA was ordinal, it allowed over 100 baseline and post baseline variables to be used.  It was done completely independently by the randomized group, by the CorCap group and control group, and of great importance to me, it was implemented by a blinded third-party.  I got my former student, Constantine Frongokis, who is a Johns Hopkins colleague of Dr. Piantadosi, who is also involved with me in the CDC Anthrax vaccine trials to implement the method that I suggested that he use.  Dr. Frongokis had no idea what the data set was about.  He had no idea which group was control, which group was treatment.  He had no idea what most of the variables even meant.  And, in fact, he had no idea even what the problem was, he was just instructed, given the data and said there are two treatment arms, and I want you to multiply impute the data using this state-of-the-art technique that was developed for the CDC Anthrax vaccine trials that we'd done, so he had no idea what the problem was, who the sponsor was, or what the treatment or control groups were.  
		It used only five multiple imputations because it's a very expensive program to run, and there's all sorts of evidence from data, like NHANES data, National Health and Nutrition Evaluation Survey, NAMSS, many other data sets that five is perfectly adequate.  Using the state-of-the-art method by a completely blinded statistician, the P value for the primary endpoint is .014, the odds ratio is 1.77, completely consistent with the previous results, except even more significant.
		When I proposed doing this, I was asked by Acorn, what's going to happen?  I said, "I don't know.  I kind of suspect that it will confirm the previous results, because typically there's little sensitivity to the particular multiple imputation model, but I will really believe the results of this one, so if this one looks bad for you guys, that's life, buy into it."  And they said well, okay, go ahead.  Do it completely blinded, and do it this way, using the best possible method.  And so it really is very much like your randomized trial, you design the trial, and what happens, happens.  We specify everything in advance, and that's what we did here, and so here are the results.  It did well for them.
		Now I want to address the fraction of percentage of missing information for the primary endpoint.  The percentage of missing information for the primary endpoint is small, and the definition of the percentage of missing information is this ratio of between imputation variance to total variance.  Anyone who has done an analysis of variance will understand this between variance to total variance, but let's suppose across the multiple imputations, as you impute different data, you kept getting the same answer, so the answer doesn't depend upon what you imputed.  That's the between variance, how much does the answer vary as you do different imputations?  So if the answer doesn't vary at all, you've got zero missing information, and the total variance is the between, plus the average within, or average within is the complete data standard error.  So under the PMA model, which I call Model Zero, there was 9 percent missing information, under Multiple Imputation SAS Model One - 5 percent, SAS Model Two - 7 percent, SAS Model Three - 16 percent, and under the state-of-the-art blinded multiple imputation model - 2 percent.  So despite the fact that there's a large fraction of missing data on NYHA, it doesn't convert to anything really with respect to the missing information and the primary endpoint.  The primary endpoint was not affected by the missing data, really, at all.
		So the effect of multiple imputation on the estimated significance of the primary endpoint, each of the four multiple imputation models confirm the conclusion of the PMA's multiple imputation model.  There's clearly a significant and beneficial treatment effect of CorCap relative to control on the primary endpoint.  The most sophisticated and blinded multiple imputation model resulted in the most significant result, the P value of .014, and odds ratio of 1.77, so my conclusion is it works.  And now I'll turn it over to Dr. Randall Starling for a clinical comment on the primary endpoint.
		DR. RAMSEY:  Just a note as you're transferring, that we're at approximately 28 minutes before the end of this session.
		DR. STARLING:  Thank you.  My name is Randall Starling.  I'm a physician and cardiologist, Vice Chairman of Cardiology at the Cleveland Clinic, and Director of the Heart Failure and Transplant Section in the Department of Cardiovascular Medicine.  I was an investigator in the Acorn trial.  I'm a member of the Steering Committee, and I am being compensated for my time and travel expenses.
		I would like to re-emphasize the primary endpoint, that it was statistically significant, and I believe clinically meaningful.  What does the heart failure patient ask of their physician when they come in consultation?  Generally, three main categories, the patient wants to feel better, the patient wants to live longer, most patients want to avoid a heart transplant, and if there's any way their own heart can get better, they're all for it.  So let's look at the components of the composite.
		These, we believe, were three clinically meaningful components.  Does the patient feel better?  Yes, and this is supported by the secondary endpoints.  Patients with the CorCap had fewer transplants and ventricular assist devices.  It should be pointed out that these advanced therapies are generally decided by committees, and not individuals.  And these types of decisions are based on objective criteria, and in some states, such as mine, Ohio, transplantation requires approval by a statewide consortium.  Finally, there is no increase in mortality, demonstrating safety to the clinician.  It should be pointed out, and this has already been stated by others, that the study was far underpowered to critically look at survival as a major endpoint.  
		A question has been raised whether bias existed that affected the major cardiac procedures.  First, the Clinical Events Committee, the details of which are in the panel packet, adjudicated major cardiac procedures.  We believe if, indeed, major cardiac procedures were withheld due to bias, it would be logical to expect more of the CorCap patients would be in Class Four heart failure, and one would expect to see an increase in mortality and morbidity as evidenced by hospitalizations.  This, in fact, was not the case.
		I'd like to lead you through this particular slide, which examines the primary endpoint at the common closing of the trial.  I'd like to point out that in the treatment group, a greater percentage of patients from New York Heart Class One through Three.  If we look at the major cardiac procedures, clearly there was a significantly smaller proportion in those treated with CorCap; yet, there was not an increase in patients with Class Four heart failure, and as already been pointed out, mortality was neutral.
		Finally, addressing the issue of investigator bias, if the major cardiac procedures were withheld, and if CorCap patients truly did not benefit, one might expect to see an increase in the composite of all-cause mortality, and all-cause re-hospitalization.  And this was not observed, as demonstrated in this graphic.  Therefore, based on my review of the data, I conclude that this is a clinically meaningful endpoint to practicing clinicians, and there does not appear to be demonstrable evidence of bias with respect to the major cardiac procedures.
		I'm going to conclude with that, and Dr. Steven Piantadosi will now come to the podium.
		DR. PIANTADOSI:  Thank you, Dr. Starling.  I'd like to conclude the discussion of the primary endpoint issues with some comments on the proper use of stratification.  The clinical and statistical rationale for stratification by MVR versus non-MVR is, in this study, a typical or classic one; that is, it was used to reduce the variance in the estimated treatment effect by controlling heterogeneity, and inducing balance of the MVR subjects in the two treatment groups.  This is essentially a no-cost way to increase the precision in detecting the treatment effect.
		The use of stratification in this classic way does not require or dictate that statrum-specific treatment effects be put forward from the trial.  In fact, under these circumstances, each stratum is expected to have different baseline characteristics, as well as outcomes.  And the study was designed to estimate the average relative treatment effect across all the strata.  Let's take for just a moment an extreme example.  If we had a randomized match pair design, each matched pair in such an experiment would be an individual stratum.  No investigator or data analyst would take the results from such a study and expect to see statistically significant treatment effects in every stratum of such a matched pair design.  The use of stratification here is exactly the same as in such a study, and if we look within strata, both favor CorCap over control.  Here's the table that you've seen before, the important point being that these two odds ratios in the MVR and non-MVR strata are consistent with the overall odds ratio.  It's obvious that they favor CorCap, but it may not be so obvious that they are statistically equivalent.
		Well, there's no real power or efficiency in this study for testing a treatment by stratum interaction.  But even if you believed that these two were different according to treatment by stratum interaction, that interaction is a quantitative one; that is, a difference in magnitude, not a qualitative one, which would be a difference in direction.  Therefore, whatever difference you believe is here, has no therapeutic consequence, and the only conclusion is that the treatment effect is clinically equivalent in the two strata.
		Now I'd like to begin the discussion of secondary endpoints with just a couple of statistical comments, following on what you've heard in the clinical context.  First, the secondary endpoints were selected for their clinical utility, as you've heard.  They were explicitly named as secondaries in the protocol, not primaries.  The protocol specified how they were to be analyzed, the time points, as well as the methodology, longitudinal regression models.  And the proper interpretation of secondaries in this sort of structured framework of a clinical trial depends mostly on the magnitude and direction of differences, not on their P values.  
		The multiplicity adjustment, which I'll discuss more in a moment, was neither necessary, nor mandatory.  The sole purpose of the multiplicity adjustment in secondaries is to provide supportive evidence to the protocol specified, and now we see statistically significant primary endpoint.  The secondaries would never be put forward as an independent basis for establishing safety and efficacy, which is the principal issue that multiplicity adjustment attempts to control.  We expect variability in the magnitude and statistical significance in the secondary outcomes.  The strict adherence to a multiplicity adjustment, as I've said, is not necessary, particularly when there is a rigorous finding in the primary.
		You've seen this information before.  I would just point out, again, briefly, that this set of secondaries protocol-specified in the classes outlined are mostly overwhelmingly magnitude and direction supportive of the primary outcome.  The individual P values are listed here, and I'll now discuss multiplicity adjustment with regard to what were labeled major secondary endpoints.  Four were pre-specified in the protocol listed under the first bullet as being major, and the protocol called for the Hochberg adjustment procedure to be implemented in response to FDA's request to specify a Type I error for them.  
		The Hochberg procedure is one that assists with the interpretation of statistical significance for multiple endpoints.  It does two things, it provides a joint success criterion for a set, in this case the set of four major secondaries, as well as individual P values for each of the components of the set.
		The manuscript, which is referenced here at the bottom, discusses testing what Hochberg calls intersection hypotheses, and what the sponsor has called joint success criteria.  And as I said, in addition, it describes how to adjust the individual P values, which is done by starting with nominal P values, ranking them, and then adjusting each one according to a very simple formula. 
		This is the result of that adjustment procedure, or the implementation of the Hochberg.  We see the four major secondaries, again, emphasizing the magnitude and direction of the treatment effects, the individual or unadjusted significance levels, and the  Hochberg adjusted levels.  Three points to note from this; first, that LVUDV meets the collective success criterion under the Hochberg procedure.  Second, the joint null hypothesis is rejected at P equals .03 according to the method outlined in the Hochberg paper.  And then, finally, it's noteworthy that LVEDV, this first secondary, would be significant also under the very strict Bonferroni-type adjustment.
		I'll now turn to Dr. Mann to discuss some of the clinical issues regarding the secondaries.
		DR. MANN:  Thank you.  My name is Douglas Mann.  I am a Professor of Medicine at Baylor College of Medicine.  I'm also a Professor of Molecular Physiology and Biophysics at that institution.  I'm also Chief of Cardiology at Baylor College of Medicine, Texas Heart Institute, and St. Luke's Episcopal Hospital.  And, finally, I'm Director of the Winter Center for Heart Failure Research, which is a translational Center of Excellence at Baylor.  What I'd like to do is address the clinical relevance of the secondary endpoints in the short time that I have.
		I think the rules on primary endpoints are relatively simple.  The rules are win or go home.  As my colleague, Dr. Jessup, indicated, the primary endpoint of the Acorn trial was met.  As Dr. Rubin stated, the statistical methodology was robust, and if anything, we probably under-estimated the P value.  What I want to do is address what's meaningful to me in terms of secondary endpoints.
		When I think about secondary endpoints, I think about three things.  As someone who's been 20 years doing basic biomolecular research on the mechanisms of heart failure, I would like to know that the mechanism, the secondary endpoint that we're looking at reflects the mechanism of the device or the drug.  We haven't spent a lot of time today talking about the mechanism for the CorCap, but it's important to emphasize that this device actually decreases the  transmural distending pressure in the ventricle, lowers wall stress, and leads to a process that we know as reverse remodeling.  This has a particular molecular signature that has been well validated over a period of 10 years, and everyone agrees with.  This is in contradistinction to procedures like the DOR procedure, and the SAVER, and the Batista, which is acute reduction in ventricular volume, which actually leads to an increase in filling pressures, not a decrease, which is what you see with molecular recovery.  So as you can see from the slide, the molecular mechanism of action of the CorCap is to unload the heart.  And you can see here that both the end-diastolic volume and the end-systolic volume decreased consistent with what we would predict the mechanism of action would be.
		The second thing I'd like to see in terms of the secondary endpoint is that it has some fidelity with other therapeutics that we know lead to molecular recovery.  And I would site here beta blockers, bi-ventricular pacers, and Ace inhibitors, all of which lead to reverse remodeling, and molecular recovery.  And, again, the secondary endpoint here with the end-diastolic volume and the end-systolic volume decreasing is consistent with that.
		I'd like to address the issue of ejection fraction.  Normally, we see a modest increase in ejection fraction with recovery, and I think my interpretation of why we didn't see that in the Acorn trial, although we did see it in the pre-clinical studies, it's important to emphasize that two-thirds of the patients here were undergoing mitral valve surgery, which actually decreases the ejection fraction, because you cut off the low impedance leak to the left atrium.  So on the one hand, two-thirds of the patients were getting an operation that decreases ejection fraction, and some were getting a procedure which would normally increase the ejection fraction.  At the end of the day, there was no significant difference in ejection fraction, although it was trending towards improvement in the CorCap group.
		The third thing that I look for in terms of a clinician scientist in terms of secondary endpoints is, what's it about to the patient?  When I sit down and talk to the patient, which I do every day, you want to tell the patient how they're going to feel, what this device or drug will do for them, you want to be able to tell the patient something clinically meaningful.  And as shown on this slide, there was a statistically significant improvement in the Minnesota Living with Heart Failure Questionnaire score.  Moreover, this was confirmed by the SF-36 scores, which also improved significantly, so there is coherence of the data in terms of quality of life issues, which I think at the end of the day what it's about for patients when we sit down and talk with them.
		Having addressed the secondary endpoints, what I'd like to do now is to turn the podium over to Steven Bolling and Michael Acker to discuss the issue of perioperative mortality.  Thank you.  
		DR. BOLLING:  Good morning.  I'm Steve Bolling, Professor of Cardiac Surgery at the University of Michigan.  I was a site PI for Acorn.  I have no ongoing financial relationship with Acorn, though I've been compensated for my time and travel.
		In your pack are discussed the surgical aspects and technical aspects, and safety issues of the procedure itself.  And of note in the MVR CorCap group, there is very good safety data.  There was an extremely low operative mortality in that group of MVR CorCap patients with an operative mortality of less than 2 percent in those very ill patients.  However, there was noted deaths early on in the trial in the CorCap no-MVR stratum.  There are actually five deaths in the stratum.  One death occurred prior to operation.  The four operative deaths are noted here.  And as we've seen, all of these patients were very sick.  They had low PPO2s, they had very large hearts, and were relatively hemodynamically unstable at the time of surgery.  These patients had predictable deaths really from instable hemodynamics.  And all of them had been operated without any type of support at that point in time.
		As we've learned how to operate on patients with heart failure, you remember 10, 20, 30 years ago when we all trained, these types of patients were not considered any type of operative candidate whatsoever.  A patient with an ejection fraction lower than 50 or 40 percent was not considered an operative candidate.  We have learned to deal with this type of heart failure patient.  And my colleague, Dr. Acker, will discuss how we learned on these patients to deal with it.
		DR. ACKER:  Hello.  My name is Dr. Michael Acker.  I am a Professor of Surgery at the University of Pennsylvania, and Chief of the Division of Cardiovascular Surgery. I'm a member of the Steering Committee for this trial.  I have no financial interest in Acorn, and I'm being paid for my time and expenses.
		I think this slide emphasizes the point that Dr. Bolling just made.  For the most part, the vast majority of the patients that had the CorCap placed alone without mitral valve surgery, it was successfully done without use of cardio pulmonary bypass or intra-aortic balloon.  What we learned early, however, that the very sick patients, the patients with very low ejection fraction, enlarged hearts, will become unstable if you manipulate, if you pull that heart up without going on bypass.  This led to hemodynamic instability, and I think ultimately led or contributed to the deaths we saw in the four early patients.
		Looking at this data as a group, on April 5th, 2002 related and discussed these deaths in detail, and decided, and recommended that in the sick patients, the very large hearts, we used cardio pulmonary bypass, we had a liberal use of intra-aortic balloon, and the data would support that this type of dissemination of information experience was successful.  Early in the trial, you can see the death rate was three out of eighteen, and after this meeting, the death rate was dramatically decreased to one out of three, or 3 percent.
		There was a second safety issue that was very prominent in the last panel meeting; and that is, the problem of adhesions or the perceived problem of adhesions, whether it represented a safety issue for patients that would need transplantation.  CorCap causes adhesions.  There's no question about that.  It causes significant adhesions, as most operations do.  I, personally, have experience with operating on two patients, transplanting patients after previous CorCap.  They were done successfully, and I had to deal with these adhesions.  As a cardiac surgeon who does transplants, almost half of our patients, and in some groups more than half, all have adhesions.  And I can tell you, the adhesions that are present, though significant, are much less than dealing with a LVAD or a bi-VAD.  
		The determination of whether adhesions influenced safety, one has to look at the results, and this slide summarizes those results.  There were seven transplants in the CorCap group, sixteen in the non-CorCap group.  There were no deaths in the CorCap group after transplantation.  All of the transplant patients are doing well.  In the CorCap, there were two deaths.  
		Adverse events are important to look at.  Per patient, you can see they're similar, so despite the adhesions being present, there were no more adverse events.  And this is true early, as well as overall experience looking at adverse events.  Importantly, if adhesions are significant as far as safety, one would expect more bleeding, initially, but we did not see that.  And I think very telling was, again, if morbidity is occurring as a result of these difficult adhesions, one would expect an increased post-operative stay.  Do not see that.  Twelve days post-operatively for a transplant after a CorCap, and almost 20 days in the non-CorCap group.  And, again, cardio pulmonary bypass was similar between groups, reflecting that adhesions were significant, but handled in all cases safely and efficiently by the surgeons.
		DR. BOLLING:  Dr. Acker and I both had opportunity to successfully operate, redo four patients who had an Acorn in place.  And truly, adhesions are a problem in all re-operations.  However, having done transplants for over 20 years, we've seen the spectrum of transplant operations change from all non-redos, to basically all redos at this time.  We've had over that spectrum of time learned how to deal with intra pericardial device placement, such as large AICD patches, such as the Acorn device, and now LVAD and Bi-VAD in almost all of our patients.  
		Clearly, there is no evidence that adhesions have significant impact upon the outcome of these patients after their surgery.  Yes, perhaps there are some longer dissection times in cases, but this issue really is effectively managed by proper surgical training, with experience of the surgical team.  
		I'm going to turn this over to Dr. Mann, again.
		DR. RAMSEY:  We're at about five minutes.
		DR. MANN:  Thank you.  I can be very brief.  The FDA in the first panel meeting presented some very graphic, albeit, anecdotal information about pericardial adhesions.  We've heard that there was really no problems in terms of the operation to the surgeons.  What I'd like to do now is address the important issue of pericardial constriction.
		First of all, it's important to emphasize that this underwent extensive preclinical testing.  There was no really no evidence of constrictive pericarditis in three separate animal models, when examined.  Second, we performed extensive echocardiographic surveillance for these patients in the study, and at no time was there consistent evidence of constrictive physiology in any patient.  Third, there's no clinical evidence of constrictive pericarditis in any of the patients in the trial, and we now have up to 331 patient years of follow-up.  And I'd just like to ask Dr. Piantadosi just to comment briefly on what that means statistically.
		DR. PIANTADOSI:  Just a brief comment regarding the precision in the estimate here of the rate of constrictive pericarditis.  Under an assumption of constant risk, which would be appropriate in this setting, the one sided upper 95 percent confidence bound on the rate of constrictive pericarditis would be approximately 1 percent per person year, so a very small risk.
		DR. MANN:  Thank you, Steve.  And, lastly, we would like to acknowledge that we cannot formally exclude the possibility that over time, five to ten years, these patients may develop constrictive physiology.  For that reason, the company has agreed to continue monitoring the patients for up to five years.  Thank you.
		I'd like now to turn this over to Dr. Starling, who will conclude.
		DR. STARLING:  Thank you.  So I want to briefly address in the remaining moment or two risk benefit from the clinician standpoint.  Question number one, is it safe?  Yes.  Mortality is neutral, adverse events have been discussed in detail by Dr. Jessup.  There is no evidence of constriction, which can be associated, as was already pointed out, with any cardiac surgical procedure.  Does it provide benefit?  Yes.  The primary endpoint was met.  There were fewer heart transplants, ventricular assist devices, and in summation, major cardiac procedures.  Patients feel better, as has been demonstrated by secondary endpoints.  There was no increase in hospitalizations, which intuitively might even be expected in a group after a thoracotomy, compared to a non-surgically treated group.
		Let's look at the specifics, functional class improved, more in the CorCap, quality of life improved, major cardiac procedures were reduced by 41 percent, and cardiac structure, as has been addressed in detail, improved consistent with beneficial reverse remodeling.  
		Finally, let me briefly address the patient population in this trial.  It was a very well treated group on evidence-based therapy, ACE inhibitors, angiotensin receptor blockers, beta blockers, as well as optimized device therapy, as was consistent with practice at that particular point in time, shown to reduce mortality, and impact remodeling.  And these patients were treated and stable for at least three months; yet, the peak oxygen consumption was 14.7 ML per KG per minute consistent with moderate to severe heart failure, with a heart size of 7.2 centimeters, 81 percent of the patients were NYHA Class III.  These were, indeed, symptomatic patients, but certainly not end-stage patients.
		Indeed, there are limited options for this particular niche of patients, and after all evidence-based medical and device therapies have been deployed, there are symptomatic patients in this group, and this therapy appears to meet an unmet need with demonstrated safety and benefit.  Thank you.
		Dr.  Ramsey, in the interest of saving time, I think I'll just conclude our presentation, thank the panel for their attention, thanks to my colleagues, consultants to Acorn, and the staff who have supported this presentation.  Thank you very much.
		DR. RAMSEY:  Thanks, Steve, and thanks to the group for keeping on time.  We now have about five minutes for our panel to ask clarification questions of the presenters.  Now if you have scientific issues or queries that aren't clarification, please hold those for the later part of the meeting.  But if something that was presented you'd like more explanation, we can do that now, quickly.
		DR. LASKEY:  Were there reasonably uniform criteria for mitral valve replacement?  And if so, what were they?
		DR. ACKER:  Yes.  Number one, the decision to replace the mitral valve was a site decision, and it was based on a site read of an echo that was greater than 2 plus MR, so 3 or 4 plus MR.  
		DR. LASKEY:  So no volumes were used for inclusion, or consideration.
		DR. ACKER:  Greater than 60 millimeters, and  had an ejection fraction less than 45 percent, but specific volumes were not calculated.  
		DR. SACKNER-BERNSTEIN:  Question about the VO2 data that were collected and reported.  I noticed in the slides it's reported as peak VO2.  I'm wondering, were those data collected, analyzed by a Core lab, are they max values?  What was done to make sure that these were values above an anaerobic threshold?
		DR. JESSUP:  Yes, there was a Core lab for peak V.02.  Each center had several tests that they sent in to the Core lab to be validated, and they were examined for the anaerobic threshold, and the maximum V.02.
		DR. CRITTENDEN:  It was my understanding that there were some mitral repairs in this group, as well, and not just replacements.  Do you have an idea of the proportion between repairs and replacements?
		DR. ACKER:  Yes.  There were approximately 83 percent of the entire group had repairs, about 17 percent were replaced.
		DR. BECKER:  In terms of the cardiac procedures, I know that bi-ventricular pacers were part of this, as well, from the documents.  I'm wondering if you can comment to me about the baseline characteristics of patients in each group in terms of how frequently patients had a wide QRS at the time of study entry for the different groups?
		DR. MANN:  First of all, as the trial unrolled, the impact of Bi-V pacing became apparent to us, so we didn't really have specific ways of stratifying based on Bi-V pacing coming into the trial.  I don't have specific numbers.  I'm going to quote off the top of my head, about 15 percent or so.  We do have them?  We can get those for you at the break.  I would like to emphasize that when we repeated the analysis, taking them out of the analysis, for major cardiac procedures it was still significant.  There was the potential, one could argue, for withholding a Bi-V pacer, so when we repeated the analysis taking them out, just looking at major cardiac procedures, still it was the transplants in the left ventricular assist devices that drove the primary endpoint.
		DR. CRITTENDEN:  The question about the decision for re-operations, this was site dependent.  Were there some grounds to make that decision?  That's part one.  And two, the major cardiac procedures following placement of CorCap were defined as those that resulted in worsening heart failure.  Do you have a list or number of all major cardiovascular procedures after placement of the CorCap?
		DR. ACKER:  We have that list.  It was the decision for transplant or VADs was a site decision based on the worsening clinical condition of the patient.  For the most part, these decisions were made by a transplant committee, not just the investigator who happened to be involved; but, rather, the entire committee made that decision, whether they had the CorCap or not a CorCap.
		DR. JESSUP:  I would also add that the slide that I showed in my presentation, in fact, listed all of what was considered the major cardiac procedures, so there weren't any extra that I didn't depict.
		DR. RAMSEY:  One question.  You had some data on all-cause re-hospitalizations, time to re-hospitalization.  Do you have data on total number of hospitalizations in the treatment of control groups?
		DR. JESSUP:  I think we can give that to you.
		DR. BECKER:  Do you want that now, or do you want that after the break?  It might take about 30 seconds to pull it up.
		DR. RAMSEY:  Yes.  We'd like to see it, so please go ahead and take a couple of seconds, if you'd like.  
		DR. JESSUP:  If you pull up Slide 86, I can show the data, 85 or 86, either one.  There you go.  This summarizes the re-hospitalization.  Let's go to 86, because that gives you the actual numbers.  So this is all-cause re-hospitalization as depicted in the treatment and the control.  Again, there was a trend for a slightly decreased re-hospitalization in the treatment, but the statistics is as can be seen.  Certainly not an excess hospitalizations in the treatment arm, again.  The point that we've been trying to make, this suggests that there was really not therapy that was being withheld.
		DR. RAMSEY:  Go ahead.
		DR. SACKNER-BERNSTEIN:  In the clinical events review committee manual, it's not clear to me what the criteria were for considering an event, a major cardiac procedure to have been due to worsening heart failure.  For example, in some cases it would require the administration of intravenous therapy.  What were the criteria that were used to define whether a major cardiac procedure was due, or were due, to worsening heart failure?  It's not clear to me.
		DR. JESSUP:  Pulling up a slide for you.  I would -- just to fill in the time.  There was a separate blinded committee that was adjudicating all of these worsening heart failure, and then we'll show you the criteria that they use.  
		DR. SACKNER-BERNSTEIN:  While we're pulling that up, I have another question.  I noticed that the common closing date for the trial was 7/4/2004.  Well, I'll get back to that in a minute.  
		DR. JESSUP:  So this was where the CERC members and Dr. Goldstein is, in fact, in this room, and this looks at the possible outcomes.  I don't know if we have a slide that actually looks at the criteria.  I'm afraid we don't have the actual criteria.  
		DR. GOLDSTEIN:  I can just say that, first of all, we were not blinded to whether the patient had mitral valve replacement or not, that was impossible to do, but we were blinded to whether the patient had CorCap.  And the three members of the committee blindedly, in a blinded manner, looked at the evidence of regression, and based upon a number of multiple factors in these patients, because they are, obviously, very sick, in general.  So it was based on clinical blinded data on each patient, whether or not there was evidence for progression during the trial, during the study.
		DR. SACKNER-BERNSTEIN:  Okay.  I'll finish the other question - the common closing date is listed as July 4th, 2004.  My understanding is that the protocol stipulated a minimum 12-month follow-up, and the last patient was enrolled in June of 2003.  July 4th seems like an odd day to have the end of trial.  Can someone explain to me why there would be a National Holiday where it's hard to get data on that date.  I mean, am I just picking on something that seems bizarre.  It's not exactly 12 months after the last patient.  Were there a cluster of events around that day that I need to ask about?
		DR. MANN:  July 4th is not a holiday in Canada, which is what drove the end of the trial, not being smug, but it was a Canadian patient.
		DR. RAMSEY:  Could you identify yourself, please?
		MR. KUBO:  Yes.  I am Spencer Kubo.  I'm Global Medical Director, employed by Acorn Cardiovascular.  The intent was to do exactly a year after June 30th, and it just seemed kind of cute to do it on July 4th.  That's all there is.
		DR. RAMSEY:  Okay.  Any further questions by the panel?  If not, we will take a 15-minute break, which will get us back here about 25 after.  We are going to try to open the partition and add more chairs for the visitors.
(Whereupon, the proceedings went off the record at 10:08:04 a.m., and went back on the record at 10:25:21 a.m.)
		DR. RAMSEY:  It is Friday, and it is the holiday season, and some of us have to fly all the way back to the left coast tonight, so I appreciate everyone very much for keeping on time.  And FDA, the Acorn people set down the gauntlet for a very nice timely presentation.  I appreciate your timeliness, now we just have to get our panel to be here.  For those of you in the back and out in the hallway, I did make an appeal to the hotel to open up that partition, but apparently, there's another meeting that's going to be starting later, and they don't seem to be willing to give that room.  So what we are going to do is during the discussion, just because the folks out in the hall can't see us, those of us - I'd ask everyone who is talking to briefly just state their name so that everyone can know who's speaking.  It also would be helpful for the transcriptionist.  I was just told there's a monitor out there.  Is the transcriptionist here?  Can they raise their hand?  Oh, do you need us to identify ourselves?  You don't.  Okay.  Well, then we -- okay.  So the panel, apparently, we don't have to identify ourselves when we ask questions, and there is a monitor so people will be able to see us.
		Okay.  With that, please go ahead.  Thank you.
		DR. YUSTEIN:  Good morning, Dr. Ramsey, and members of the Dispute Resolution Panel.  My name is Ron Yustein.  I'm the Clinical Deputy Director for the Office of Device Evaluation in the Center for Devices and Radiological Health. On behalf of ODE, as well as FDA's Division of Biostatistics, I'd like to welcome the panelists, and also thank you ahead of time for your efforts and time in reviewing this very challenging issue.
		Today we will be presenting a summary of our FDA's review and recommendations for the Acorn CorCap Cardiac Support Device.  Making FDA's presentations this morning will be Dr. Bram Zuckerman, our Director for the Division of Cardiovascular Devices in the Office of Device Evaluation; Dr. William Maisel, Assistant Professor of Medicine at Harvard Medical School, and current Chairman of the Circulatory System Devices Advisory Panel; Dr. Ileana Pina, a heart failure cardiologist and Professor of Medicine at Case Western Reserve University in Ohio. Dr. Pina also serves as a consultant to FDA and CDRH.  Dr. Laura Thompson, a statistician and member of the Division of Biostatistics in the Office of Surveillance and Biometrics, and Dr. Clyde Yancy, the Medical Director and Chief of Cardiothoracic transplantation at Baylor University in Texas.  Dr. Yancy was one of the two primary panel reviewers in the June 2005 Advisory Panel for this submission, and also has been fully participating in FDA's post panel review of this PMA.  Finally, I will close with some brief recommendations and conclusions regarding the submission from the Office.  
		With that, I'd like to turn the microphone over to Dr. Bram Zuckerman, who will provide an introduction to FDA's review of the Acorn CorCap device.  Bram.
		DR. ZUCKERMAN:  Thank you, Dr. Yustein, and thank you, panelists, for your time today.  Here is a picture of the CorCap which has been described in the sponsor's presentation.  These are the current proposed indications for use.  The indication statement is based on the post hoc subgroup analysis referred to as the focused cohort analysis.
		There was extensive interaction between FDA and Acorn throughout the review of the IDE and PMA.  Currently, there are key points of disagreement regarding the history of this process.  While FDA is most interested in focusing today's discussion on the interpretation of the final clinical trial results, we would like to clarify some of the events that transpired during the review process.
		The primary endpoint for the Acorn trial was a composite of mortality, the need for additional major cardiac procedures, and change in NYHA class.  Fifty-eight percent of patients did not have a blinded NYHA assessment at baseline.  In the sponsor's panel pack and presentation, they have omitted key details regarding the reasons for such a high proportion of missing NYHA data.  
		I will begin with FDA's approval of expansion to a pivotal trial in June 2001.  Our approval letter included several significant future concerns related to the primary endpoint.  Despite FDA's concerns with Acorn's choice of primary endpoint, the sponsor began enrolling patients in their trial.  Contrary to what Acorn has stated in their panel pack, the primary endpoint always included a blinded assessment of New York Heart Association functional class.  During discussions to resolve FDA's concerns regarding the primary endpoint, the sponsor chose to change the assessment methodology for blinded NYHA from the Goldman method to the current Kubo methodology.
		Due to Acorn's decision to change assessment methods, FDA expressed concern regarding how Acorn intended to handle the missing blinded NYHA data in the 41 patients who had already been enrolled prior to Acorn's decision to use the Kubo NYHA methodology.  Acorn assured FDA that missing baseline data would not be an issue.  They believed that baseline assessment by the site investigator would not be affected by treatment bias, since it was performed prior to randomization.  The resulting analysis plan for the NYHA component and the revised primary endpoint included a comparison of the site assessment at baseline with the last available blinded core lab assessment using the Kubo methodology in all patients.
		While there were only 41 patients enrolled in the trial when Acorn made the initial decision to switch to the Kubo blinded NYHA methodology, Acorn continued enrolling patients throughout these discussions.  As a result, 172 patients were enrolled prior to implementation of the new blinded assessment of NYHA.
		Further complicating the analysis plan, the sponsor informed FDA in March 2004 that the agreement between site and core lab NYHA was only 35 percent.  This was much lower than the agreement demonstrated in the sponsor's initial validation study.  Due to the poor correlation between site and core lab NYHA values, Acorn proposed that it would be more scientifically valid to use site NYHA measurements at both baseline and follow-up for the primary endpoint.  Based on this new information, FDA agreed that using a comparison of site and core lab was not ideal.  However, since all patients were already enrolled, and the study was only a few months from completion, we were uncomfortable at the time with changing the primary endpoint, especially to incorporate a subjective, unblinded measure, such as site NYHA, given the unblinded nature of the trial.  
		FDA recognized that because the sponsor had chosen to continue enrolling patients despite a lack of agreement on the primary endpoint, the missing NYHA data created a difficult situation.  In an attempt to make the best of a sub-optimal situation, FDA proposed that Acorn use an imputation model as a possible way to recover the missing blinded NYHA data.  We also requested that the sponsor analyze the NYHA component using available data.
		Acorn has claimed in its panel pack that imputation was the pre-specified analysis plan for the NYHA component of the primary endpoint.  In truth, the sponsor rejected the suggestion of imputation, stating that while mathematically possible, imputing such a large amount of missing data would not be seen as clinically valid by the scientific community.  Please refer to Acorn's Supplement 45, response to Question 1, which is found as Attachment 19 in your FDA panel pack for verification.
		Acknowledging that it was impossible to come to an agreement regarding the best analysis plan for the NYHA component, FDA recommended that the sponsor analyze the NYHA component according to as many methods as they felt were appropriate, and that FDA would take into account all analyses in our review of the PMA.  Please refer to Attachment 21, the FDA response letter to Acorn's Supplement 45 for verification of the statement.
		Two months after key members of Acorn were unblinded to the study results, Acorn reversed its stance regarding imputation, agreeing to use it as a method for analysis of the primary endpoint results.  Revision 8 of the clinical protocol was the first to include any mention of imputation.  The protocol was not reviewed by FDA prior to our receipt of the PMA.
		FDA would also like to clarify events that took place during our review of the PMA.  As part of FDA's review of the sponsor's PMA, the results of the Acorn clinical trial were presented at an Advisory Panel meeting.  After a rich discussion, the panel voted 9-4 in favor of a not-approvable decision for the PMA.  The Panel Chair, Dr. William Maisel, will provide a more detailed account of the meeting shortly.  
		Following the panel meeting, FDA and Acorn held several meetings to discuss how best to proceed.  In an effort to address concerns raised by the panel and FDA, Acorn proposed to conduct a re-analysis of their data in an attempt to find a patient population in which the risk benefit profile of the device was maximized.
		While FDA found this idea interesting, we cautioned the sponsor that a post hoc analysis may not be sufficient for device approval.  FDA told the company that it was more likely they could use such a re-analysis to identify a population for an additional confirmatory clinical trial.  FDA issued a not-approvable letter in August 2005, citing concerns regarding safety and effectiveness of the device.  We also listed three possible options for the sponsor to address these deficiencies.  Each of these options included post hoc re-analysis of the 300-patient data set.  However, FDA indicated in both a letter and several meetings with the sponsor that we have concerns with the two approaches that relied solely on post hoc subgroup analyses.
		In meetings with the company, FDA consistently emphasized that a post hoc re-analysis would need to be prospectively validated with additional clinical data as described in Option C of our not-approvable letter.
		Despite these warnings that a prospective study would be needed for device approval, Acorn submitted only a post hoc subgroup analysis in response to our not-approvable letter.  This is referred to as the focused cohort analysis.  This analysis examined 19 baseline covariates and their relationships with eight clinical outcomes in order to identify the subgroup that received the greatest incremental benefit from the CorCap.  No substantive new patient data have been provided to FDA since the Advisory Panel meeting.
		While FDA found the focused cohort analysis to be provocative, we maintain that this exercise was hypothesis-generating in nature, and needs to be validated with prospective clinical data.  This position was communicated to Acorn in a not-approvable letter sent in February 2006.  
		Now that I have reviewed the file history, I would like to go through the key scientific concerns that led to our not-approvable decisions.  We will expand on each of these points throughout our presentation today.
		One, for a variety of reasons, the primary composite endpoint result is not interpretable.  Two, the secondary endpoint results are problematic and not supportive of trial success.  Three, the safety concerns raised by FDA and the Advisory Panel, including perioperative mortality, added complications with re-operation, and the potential for pericardial  constriction were not adequately addressed by the data presented from this study.  Four, pre-specified subgroup analysis of the MVR and no-MVR strata do not indicate that there is a subgroup where the risk benefit profile of the CorCap is optimized in relation to the 300-patient cohort.  And, finally, five, the focused cohort analysis may have identified a target population in which the risk benefit profile of the CorCap is improved.  However, the results of this post hoc analysis do not constitute valid scientific evidence that the CorCap is safe and effective.  In order to support device approval, these results must be prospectively validated in an additional clinical trial.  
		Dr. William Maisel will now come to the microphone.  He is currently the Chair of the Circulatory Systems Device Panel, and will discuss the June 2005 Acorn Panel meeting.
		DR. MAISEL:  Good morning.  My travel is being paid for by the FDA today, but I have no other conflicts.
		The Circulatory System Device Panel met on June 22nd, 2005 to consider the Acorn CorCap cardiac support device, and I'd like to try to summarize the results of that panel meeting.  My comments are specifically about the panel meeting, and do not pertain to any interactions that may have occurred between the sponsor and the FDA after the panel meeting, or to any data analysis that may have occurred after the panel meeting.
		The Circulatory System Device Panel for this meeting was comprised of 15 participants with diverse expertise, including several cardiac surgeons, interventional cardiologists, heart failure specialists, statisticians, a consumer rep, and an industry rep, and the panel voted not approvable by a 9-4 vote.  
		There were a number of panel concerns, and I will try to summarize them briefly, as we had an eight hour meeting, and I have about eight minutes to tell you about the meeting.  The panel concerns included device effectiveness, including both primary endpoint and secondary endpoint issues, safety concerns, and I'll address other issues, such as missing data and subgroups.  I think one of the take-home messages from the panel meeting and from my summary of it, is that there was no one issue that was the deal-breaker, and I'll try to make that point.  In the end, the panel felt there was an absence of reasonable assurance of safety and effectiveness.
		As you're well aware, the primary endpoint is a composite endpoint combined of New York Heart Association Class, major cardiac procedures, and mortality or death.  The overview of the main issues is, for the New York Heart Association classification, as you know, there was a high rate of missing data, and the panel questioned the clinical significance of the core lab New York Heart Association classification.  Major cardiac procedures were the driving force of the primary endpoint results, but there was concern that this is a biased endpoint, and there was no statistical difference in overall mortality, but there was a high early surgical mortality rate.  I'd like to cover each of these issues in a little bit more detail.
		As you're well aware, the New York Heart Association classification baseline data for core lab was missing in 174 out of 300 patients, which is well over 50 percent.  Data was imputed for the primary endpoints, and only 104, because approximately 70 of the patients met the primary endpoint for other reasons.  I won't belabor this point. I'm sure there'll be robust discussion on this issue by the panel today.  
		What I would like to highlight is that there is an issue regarding clinical relevance of the core lab New York Heart Association classification.  I don't think any heart failure doctor, or anyone who takes care of patients would argue that actual New York Heart Association classification is meaningful, and that improvements in that classification are meaningful.  When you start talking about a core lab with blinded assessment, I think we're moving a little bit away from actual New York Heart Association classification, and the correlation between those two is not perfect.  And then the concept of adding imputed core lab New York Heart Association classification, which introduces more uncertainty regarding the actual values that were measured, we're moving further and further away from actual New York Heart Association classification.  And this was a concern of the panel.
		I will also note that the sponsor statistician, Dr. Brown, at the first panel meeting said, "It is a lot of missing data.  This is hard to assess."  There's no question that the panel struggled with this issue. I think it is a misconception to imply that the panel did not understand the issue, or that there was some important misunderstanding regarding the more than 50 percent missing baseline core lab data.
		And, finally, I just wanted to make one comment, as the panel did address the FDA versus sponsor responsibility for the missing data.  Ultimately, the sponsor is responsible for the design of the study.  We can debate the quality of the study design.  I certainly think an unblinded New York Heart Association classification for a major device trial is not appropriate.  Ultimately, it is the sponsor's responsibility for the design, but in the end, it doesn't matter whose fault it is.  There's a lot of missing data, and the data must support safety and effectiveness.
		The major cardiac procedure endpoint was also troubling for the panel.  There are fewer in the treatment compared with the control, but there is a strong bias against intervening in the CorCap group, secondary to concerns about re-operation or potentially secondary to concerns about re-operation.  There were fewer transplants and ventricular assist devices placed in the CorCap group, fewer repeat mitral valve surgery, fewer bi-ventricular devices.  Bi-ventricular devices were included as a major cardiac procedure, although as the sponsor has already pointed out, removing them from the analysis doesn't change the final analysis.
		There was concern that the decision making regarding major cardiac procedures is subjective, and I don't think you can get around that issue.  That's appropriate, physicians taking care of their patients make the right decision, but the panel was very concerned that the decision to send someone for another procedure was influenced by the presence of the CorCap.  And while the endpoints were adjudicated by a blinded committee, the decision making itself was not blinded.
		And then, finally, there was no difference in mortality, but there was a learning curve that was not over one case, it was over years.  And as an example of the no-MVR stratum operative mortality as shown here in year one, the operative mortality was 16.7 percent, in year two 10 percent, in year three it was zero percent.  Certainly, that's an encouraging trend. I think the panel had some concerns about that, however.  We've also heard about some operative changes that were made that may account for this decrease, so Dr. John Somberg, who was a panel member, said, "I think we have a serious adverse event on up- front profile with this device."
		There were a number of secondary endpoints, and while we've heard the argument that the missing data for the primary endpoint is for a particular reason, there's also substantial amounts of missing data in the second endpoints, which are of concern.  Peak VO2 and six-minute walk, which are the most objective measures of exercise, were missing in sicker patients.  This was not at random, so the comparisons between the groups are not necessarily relevant, and there is concern about the missing data.  BNP was higher in the treatment than in the control groups.  And, supposedly, these were sick patients, but 55 percent of patients had a BNP that was in the normal range.  And then there are obvious issues with quality of life in patients who were not blinded to their treatment.
		While I already highlighted some of the safety issues, including the early mortality risk, the morbidity from surgery, difficulty with re-op we've heard about.  And one of the points I wanted to make, and that the panel made, is that these study patients are not end-stage.  These aren't cancer patients who are dying and have no hope.  One-third of control patients got better, 55 percent of BNP was in the normal range.  There's a real concern about harming patients who otherwise might do better, or do okay.
		The subgroup analyses, as we know, were hypothesis-generating, but the panel was interested in trying to find a group of patients in whom this device might actually benefit.  The ischemic versus non-ischemic patients are interesting.  The majority studied had non-ischemic cardiomyopathy.  Because of concerns regarding future revascularization, the sponsor has appropriately spelled out exactly which patients should not be considered if they have ischemic heart disease, such as those who might need revascularization in the future.  But, again, the majority of these patients were non-ischemic.  The MVR versus no-MVR strata were pre-specified.  But as I already mentioned, the operative mortality was high, and Dr. Mariell Jessup, who was on the Steering Committee and is here today, commented during the first meeting, "Clearly, the operative mortality rate in the no-MVR stratum was of concern."  So the panel considered is there a viable subgroup or non-ischemics undergoing MVR, a possible subgroup for this device, and the concern was that effectiveness appears less in the MVR compared to the no-MVR group.  The study was underpowered to detect important differences between these groups, and the ejection fractions were different in the two groups, as well.
		So, in the end, there were a number of safety and effectiveness concerns for the panel, including the New York Heart Association missing data, the clinical relevance of the core lab high early mortality primary endpoint issues, no evidence of a mortality benefit, and we've covered all of these points.  Again, the message here, obviously, is that this was not a one trick pony, there wasn't one issue that was the deal-breaker.  And so, in the end, the panel voted not-approvable by a panel vote of 9-4, because of concerns about effectiveness and safety.  It was not one issue that was the key issue.  There was additional data from -- the panel recommended additional data from randomized trials were needed to support device approval.
		At this point, I'd like to introduce Dr. Ileana Pina, who is Professor of Medicine at Case Western Reserve University, and a Heart Failure Specialist, who will talk to us about the FDA clinical review.
		DR. PINA:  Thank you, Dr. Maisel, and I appreciate the opportunity to be here today, distinguished panel, ladies and gentlemen.  
		Just to briefly review, you've seen this before, this is the general structure of the trial with 300 patients, 193 in the MVR stratum, with 107 in the no-MVR stratum.  The MRV stratum was chosen for randomization from patients who had already been deemed as candidates for MVR, and we can discuss this later in the afternoon.  A large number of the MVR stratum were entered in five of the top enrollment sites.  
		The primary composite endpoint, which you've also heard before, consisted of mortality, the need for major cardiac procedure due to worsening heart failure, and a change in New York Heart class.  A comparison was made between treatment, namely CorCap, and control, based on the outcomes of improved, same, or worsened.  A patient was defined as worsened if they died, had a major cardiac procedure, or had at least one class increase in New York Heart class.  A patient was considered improved if they were alive, did not need an additional procedure, and decreased by at least one New York Heart class.  All other patients fell into the category of same.
		Dr. Zuckerman has already introduced the main concerns of the FDA.  I will first talk about the primary endpoint result not being interpretable.  Complicating our interpretation of the primary endpoint are questions regarding the clinical validity of the core lab New York Heart measurements.  As illustrated in this table, there was only 35 percent agreement between the New York Heart class determined by the site investigator and that assigned by the core lab in the 126 patients with both measurements at baseline.  Out of the 26 patients who were deemed to be Class II by the site investigator, 15 were deemed to be Class III by the core lab, and an additional 8 deemed as Class IV.  Of the 96 patients that the site had classified as Class III, 51 were classified as Class IV by the core lab. 
		The baseline characteristics for patients enrolled in this trial, such as an ejection fraction of 27, a peak VO2 of 15, a six-minute walk of 340, and a BNP under 100, are traditionally associated with New York Heart Class II and III heart failure; and, therefore, it appears that the core lab methodology overestimates the sickness level in these patients.  It is unclear what the core lab New York Heart assessment is actually measuring, raising the issue of how to clinically interpret the results of the primary composite endpoint when using New York Heart class data.
		As Dr. Zuckerman has described, 58 percent of the patients were missing the blinded New York Heart assessments at baseline due to the sponsor's decision to continue enrolling patients in their trial prior to reaching an agreement on the primary endpoint.  This, coupled with a lack of correlation between site and core lab New York Heart measurements presents significance challenges for data interpretation.
		The four analyses listed in this table have been discussed at one point or another, none of which are without their own limitations.  The final protocol approved primary endpoint, which you see here in the lower line, included a comparison of site-assessed New York Heart class at baseline, to the core lab at follow-up.  As discussed on the previous slide, this comparison is not scientifically valid due to the low correlation between the two instruments.  The primary endpoint could also be analyzed using site New York Heart assessments at baseline and follow-up.  These measurements were available, as you can see, in the majority of patients, but site-assessments may be subject to treatment bias in an unblinded trial.  Even so, it is worth noting that the result of the primary composite is not statistically significant when using the site-assessed New York Heart class.  The sponsor has also analyzed the primary endpoint by imputing the missing core lab data for 35 percent of patients.  While the statistical methodology may be sound, the clinical validity of the core lab New York Heart class has not yet been demonstrated.  
		We also present here an analysis on the second line that includes all patients with an outcome for the primary composite endpoint; that is, patients would have either died, had an additional major cardiac procedure for worsening heart failure, or have core lab New York Heart assessments at both baseline and follow-up.  
		The uncertainty surrounding the core lab New York Heart methodology, and the fact that using available data does not yield a significant result has left us with more questions than answers regarding the primary composite endpoint.  In an effort to fully understand these data, we have also taken a look at the individual components of the primary endpoint.
		The table here parallels that one that you just saw on the previous slide, with each row now corresponding to a different method for analyzing the New York Heart class component.  On this slide, we show the average treatment difference observed over time, only on the New York Heart class component.  A clinically significant treatment difference in New York Heart class was pre-specified by the sponsor to be .5 class.  As you can see, all of these analyses resulted in a difference of less than .1 of a class between treatment and control.  Therefore, we are unable to conclude that the CorCap provides a clinically meaningful treatment effect in terms of patient functional status, as assessed by the New York Heart class.  These tables are adapted from the Executive Summary.  You should be able to follow them there.
		The trial showed similar mortality results.  You've also seen this prior to this slide.  The sponsor has indicated that changes in LV dimensions are, indeed, clinically meaningful as they have been correlated to a mortality benefit in previous trials, such as beta blocker drug trials.  It is well accepted that true reverse remodeling should be linked to favorable survival benefits.  Therefore, with a lack of mortality benefit seen in this trial, we are left to question whether or not the CorCap is associated with true reverse remodeling.
		A major cardiac procedure was defined in the protocol as a transplant, an LVAD or left ventricular assist device, cardiac re-synchronization therapy, also known as BiV pacing or CRT, coronary bypass graft, mitral valve repair or replacement, or tricuspid valve repair or replacement.  All CRT, MVR, and TVR procedures were adjudicated by the Clinical Events Committee to determine whether the procedure was related to progressive heart failure.  All transplants and LVADs were automatically counted as major cardiac procedures indicative of worsening heart failure, and were not adjudicated.  The spirit of the definition was to identify cardiac procedures that were due to worsening heart failure, as opposed to those needed to correct an inadequate and failed surgery.
		Cardiac re-synchronization therapy or CRT became available during the study.  CRT insertion is presumably prompted by worsening heart failure, a wide QRS of greater than 120 milliseconds, and appropriately maximized medical therapy.  In the graph displayed here, the CRT implants are represented in the light bars, and the open procedures are represented in the red bars.  While there were more CRT implants in the control group, there was not a significant difference between the two groups for the total population.  The observation that control and treatment patients had similar rates of CRT implants, which is a catheter-based procedure, suggests that the two groups had a similar degree of worsening heart failure.  A consistent result was not observed when looking at the open heart procedures.
		In an effort to understand what causes this imbalance, we have examined the major cardiac procedures by strata.  In the MVR stratum in which all patients underwent an open chest procedure at baseline, the number of CRT implants was nearly identical between the treatment and control.  In addition, there was only a slight increase in open heart surgeries performed in the control group when compared to the treatment.
		Now let's take a look at the no-MVR group.  A quick reminder that the control patients in the stratum had no operations at baseline.  Here we observed that a significantly higher number of control patients received open heart surgery than the treatment patients.  The possibility of a referral bias due to technical difficulties associated with the presence of the CorCap is raised by these conflicting outcomes.  If the CorCap was providing a treatment effect, a similar decrease in CorCap patients needing CRT should have been observed.
		For all these reasons, FDA is concerned that the major cardiac procedures component may be biased in favor of the CorCap.  At best, whether treatment bias exists in this unblinded study is not clear.
		In summary, the FDA has concerns about the primary endpoint due to the large amount of missing data, the lack of established validity for the core lab questionnaire, and the fact that substituting site NYHA for the primary endpoint analysis yields an insignificant result.
		Furthermore, there is no observed benefit in mortality or New York Heart class, and the only sign of a potential clinical benefit is the major cardiac surgery component in the no-MVR group, a result which may be confounded by treatment bias, and placebo effect.  For these reasons, FDA believes the primary endpoint result is not interpretable.
		Due to the complexity of device trials, these device trials are relatively small and not powered to definitively examine objective, clinically meaningful endpoints such as mortality, as we see in the Phase III studies investigating safety and efficacy of new drug therapies.  Device trials often rely on surrogate endpoints in order to maintain a least burdensome approach.
		Under this paradigm, secondary endpoint data are important to consider when determining the risk benefit profile of the device that's under review.  It is expected that the totality of the data should support the device approval.  Given the uncertainties surrounding the primary endpoint in the Acorn trial, the consistency of secondary endpoint data is especially important to examine.  The sponsor pre-specified four major secondary endpoints, which you see here on this slide, chosen to represent a spectrum of functional, physiologic, and structural changes by which the medical community could evaluate the effectiveness of the device.  The Hochberg method was utilized to adjust for multiplicity in an effort to control Type I error.  After this adjustment, the only P value that can be declared statistically significant corresponds to the LVEDV, or end-diastolic volume.  
		The FDA has consistently maintained that showing improvement in structural endpoints alone would not be enough to support device approval.  In other words, it is not sufficient to show that only the CorCap can physically confine the heart.  There must also be a functional benefit.  The results of this major secondary endpoint analysis serves as a prime example of the inconsistent results found in the study.  The sponsor was able to show improvement in structure by applying a physical constraint, LVEDV, without corresponding clinically or statistically significant improvements in the physiologic parameters, such as ejection fraction, or patient function, such as Minnesota Living with Heart Failure, or New York Heart Class.
		At one point in time, the five endpoints that are listed on this slide were the primary endpoints for this trial.  At the time the FDA asked the sponsor to propose clinically meaningful treatment differences for these endpoints.  Although the primary endpoint was subsequently changed, all of these parameters remained important and meaningful when assessing the effectiveness of a CorCap.  As depicted in this table, the CorCap did not demonstrate a clinically meaningful treatment difference in any of these five endpoints.  While we would consider a drop of .5 in New York Heart Class to be significant, the New York Heart Class as reported here and discussed earlier by me decreased by less than .1.   The Minnesota Living with Heart Failure Questionnaire is a subjective measure of patient quality of life.  The minimally clinically significant difference in this endpoint is generally considered to be a decrease of five or more points.  The fact that patients did not improve even by that much in this unblinded trial is a cause for concern.
While some of these parameters were presented by the sponsor to have low unadjusted P values, it is important to note that statistically significance does not always imply clinical significance.
		FDA would also like to examine the results of the exercise testing data collected in the study.  This figure shows the average change in six-minute walk over the first twelve months.  This is based on available data.  On available data, the control group improved by almost 22 meters more than the CorCap patients.  The sponsor has indicated that there is a large amount of missing data for the six-minute walk, with more data missing in the control group.  FDA also notes that if we only look at CorCap patients who participated in the six-minute walk, they had an average improvement of less than 20 meters, which is not considered clinically significant.
		In a similar fashion, this type of graph shows us the peak VO2 data for available patients.  The control group remained relatively stable across time, while the CorCap decreased by .6.  Again, data interpretation is confounded by the level of missing data.  Regardless, the fact that CorCap patients who have peak VO2 data experienced a steady decrease from baseline, indicates that the CorCap did not elicit a clinically meaningful improvement in peak VO2.
		This table now displays the treatment difference observed in various structural endpoints now averaged over the first 24 months of the trial.  While the CorCap was associated with the expected reductions in end-diastolic volume, the absence of a significant improvement in ejection fraction challenges the proof of concept, and raises a question of true clinical benefit.  Dr. Mann has stated that the possible reasons for this lack of change of ejection fraction is the fact that MVR patients can drop their ejection fractions after surgery.  In fact, in the no-MVR group, the ejection fraction actually decreased, and the treatment difference was negative.
		We're also impressed by the magnitude of missing data from the secondary endpoint, noting the peak VO2 data are missing in 35 and 49 percent of treatment and control.  These positive results could be very extremely problematic.  
		This slide shows a finding that has been repeated in the literature again and again, that there is no correlation between changes in structural and functional endpoints.  The sponsor and FDA have examined various combinations of structural and functional endpoints with the resulting plots looking very similar to those that I'm showing you here.  
		In review, there is a lack of clinical or statistical significance in the majority of key structural and functional measures.  Similar to the primary endpoint, there are a large amount of missing data for several secondary endpoints.  Also, functional endpoints result favor the control group when using available data.
		Based on the analysis conducted by both the sponsor and FDA, there is no evidence of changes in cardiac structure have led to meaningful improvements in physiologic parameters, patient function, or quality of life.  For all these reasons, the FDA believes that the secondary endpoint results are problematic, and not supportive of trial success.
		There are also several safety concerns raised by the FDA and the Advisory Panel that have not been adequately addressed by the data provided.  First, the perioperative mortality rate for patients receiving the CorCap in the no-MVR group is almost 8 percent.  Alternatively, zero patients in the control group died in the first 30 days.  The upper 95 percent confidence interval limit is 19 percent.  
		The FDA believes this rate is unacceptably high in light of the uncertain benefit experienced by the patients in this study.  FDA has included in your panel pack the operative reports for re-operations in patients receiving the CorCap, as well as those who only had mitral valve repair or replacement at the time of surgery at baseline.  
		While the sponsor has been quick to point that adhesions are mentioned in the reports for both of these patient groups, the FDA believes that there is a clear distinction between the level of detail describing these adhesions, as well as the difficulty associated with their dissection.
		The FDA and Acorn have both previously agreed that patients receiving this device would be ineligible for future bypass surgery.  This is an established procedure with proven clinical benefits, and it is impossible to predict who would need bypass surgery in the future.  
		The issue of pericardial constriction has been covered.  We realize that this is a time-dependent effect, but based on the adhesions that have been found, this is something that really needs to be considered in the future.
		Given the fact that patients were randomized into two strata based on their need for mitral valve surgery prior to study enrollment, it is also important to look at the study results of the individual strata, which was a pre-specified subgroup analysis.  		In the MVR cohort, which included almost 200 patients, the incremental benefit of the CorCap placement was lower than that seen in the overall trial results now seen in the lower two lines here.  While the overall composite results appear stronger in the no-MVR stratum, a closer look brings us back to the point that the major cardiac procedure component of these 107 patients played a major role in driving the statistical significance.  In addition, the high perioperative mortality rate raises questions regarding the overall risk benefit profile in these patients.
		Finally, I will briefly discuss FDA's concern with a focused cohort analysis.  This post hoc analysis is interesting, and it is provocative, in that the sponsor may have, in fact, identified a patient population in which the risk benefit profile was increased.  However, this finding needs to be prospectively validated with additional data and clinical trial.  We need to remember that in previous heart failure trials of pharmacotherapy, we have seen cases where subgroup analysis that have generated hypotheses have not proven to be positive.  The best two examples were the Elite I and Elite II trials, where the Elite I trial pointed to improvement in survival with the drug Valsortan.  And when studied prospectively, this was not the case.  In a similar fashion, Crace I and Crace II, Crace I raised questions about Mlodipine in the dilated cardiomyopathy group, which when looked at prospectively, again, did not bear truth.
		I will now introduce Dr. Laura Thompson, who is the Mathematical Statistician in the Division of Biostatistics for the FDA, and she will be presenting the statistical review of the trial.
		DR. THOMPSON:  Thank you, Dr. Pina.  Regarding the five concerns that have been brought up by the other speakers, I will be discussing FDA Concern One, Two, and Five, beginning with Number One, the primary endpoint result is not interpretable.
		For reference, I give the primary composite endpoint definition in this slide, and this is the three components, as well as the ordinal scoring of improved, same, and worsened.  The patient was improved only if they improved on NYHA, and didn't die or have an additional major cardiac procedure.  They were worsened if they died or had an additional major cardiac procedure, or worsened on NYHA.  Otherwise, they didn't change.
		I'd like to now give an overview of some of the history related to how the missing data came about, but from a perspective where it affects statistical analysis.  We heard from Dr. Zuckerman that the sponsor had begun their trial before agreement on the primary endpoint.  By the time the current NYHA instrument was introduced, 58 percent of the patients had begun their follow-up, and missed the measurement. One possible alternative at the time was to use the standard unblinded site physician-assessed NYHA at baseline, in place of the missing core lab NYHA.  Because the assessment was made prior to randomization, FDA and the sponsor felt that it could serve as an adequate replacement for the missing values.  
		Here is the analysis of the primary endpoint where site-assessed baseline NYHA replaces core lab baseline NYHA for all patients.  The estimated odds ratio is 1.45, estimating a 45 percent probability of being in a better category for CorCap over control.  P value is .12.  However, as we've heard from Dr. Pina's presentation, the agreement between site-assessed NYHA and core lab NYHA at baseline is low.  At that time, the sponsor asked to switch the NYHA measurement from core lab to site-assessed for both baseline and final follow-up.  FDA didn't believe this was a good idea, because the trial was almost finished.  And, furthermore, site-assessed NYHA is an unblinded assessment.  Here are the results from that analysis, replacing core lab NYHA with site-assessed NYHA at both baseline and follow-up for all patients.  The estimated odds ratio is 1.51.  P value .07.  
		At this time, FDA proposed multiple imputation as a way to handle the missing data.  Data appeared to be missing at random due only to a design feature; that is, baseline NYHA instrument was unavailable, and not apparently due to outcome.  So the main assumption for multiple imputation, missingness at random, appeared to be reasonable to make.  In addition, FDA requested to see the primary endpoint analysis using complete data.  
		As mentioned by Dr. Zuckerman, the sponsor rejected the recommendation to use imputation, but after data were unblinded, agreed to use it.  FDA feels that it is important to decide on the primary analyses for a clinical trial prior to data unblinding in order to avoid any suspicion of having looked at the data prior to finalizing primary analyses.  
		Two imputation models were submitted by the sponsor for FDA review.  The imputation models are similar in that they regress baseline NYHA on observed variables to get a predicted value for the NYHA class.  All models used the same data to build the imputation model, and all models used multiple imputation techniques, where up to 100 imputations were done, and the estimate for treatment effect was averaged over the imputations.
		Additionally, all models assumed missingness at random, which appears to be a reasonable assumption here.  So the results from the imputations are similar.  In total, 36 percent of CorCap, and 32 percent of control primary endpoint values were based on imputation.
		On this slide, I present results from one of the models submitted to FDA by the sponsor.  This is the analysis that the sponsor presented as their primary analysis, which gives an estimated odds ratio of 1.73, P value 0.024.  And as I mentioned before, FDA also asked the sponsor to provide an analysis using all patients who had the available baseline core lab NYHA.  This analysis gives an estimated odds ratio of 1.75, P value 0.12.
		Although the primary endpoint analysis was only appropriately powered to detect a significant treatment effect in the composite, the elements of the composite were looked at individually in order to determine which components might contribute relatively more.  Toward this end, I will present separate analyses of each of the components.  Note that because the family-wise error rate was not controlled a priori for these components analyses, the P values that are presented are not interpreted in the same way as for the primary endpoint.  The significance level with which to compare the P values is not known.  Nonetheless, we can still examine them individually to see which components contribute the most to the overall composite.
		First, in a separate analysis of mortality, a log-rank test of the difference in Kaplan-Meier survival curves up to the common closing date give a P value of .85.  There were 25 deaths in each group up to the common closing date, but the CorCap group had more deaths prior to 30 days.  Because mortality was identical between groups at the common closing date, this endpoint doesn't contribute much of anything to the composite endpoint, and there is no apparent CorCap benefit in mortality.
		This table gives percentages of major cardiac procedures by treatment group.  There were 22 percent of control patients with additional major cardiac procedures, and 12.8 percent of CorCap patients.  A test comparing the two groups found that control had significantly more additional major cardiac procedures, so it appears that the number of patients who received additional major cardiac procedures contributes a great deal to the statistical significance of the composite result.
		A separate analysis of the change in NYHA component of the primary endpoint looked at the average treatment difference over time.  I show results using imputed NYHA baseline class, as well as results using available data.  From the results, we see that imputing missing data doesn't change the non-statistically significant result.  NYHA is likely not responsible for statistically significant results in the primary analysis.  Additional major cardiac procedures is mainly responsible for the significant result. 
		Secondary endpoint results are problematic and not supportive of trial success.  There were four pre-specified secondary endpoints.  These were left ventricular end-diastolic volume, left ventricular ejection fraction, Minnesota Living with Heart Questionnaire, and site-assessed NYHA.  The Hochberg procedure was prospectively proposed for these endpoints to control family-wise Type I error rate at 5 percent.  The Hochberg procedure is used to adjust the individual P values for multiplicity.  We need to adjust for multiplicity when testing multiple endpoints, because the probability of finding at least one significant endpoint just by chance increases with the number of endpoints tested.  In the following slides, I present the individual P values adjusted for multiplicity.  Because they are adjusted, these P values can be compared to a .05 criterion.  
		First, I'd like to present the following reminder regarding testing multiple secondary endpoints to support regulatory claims once the primary endpoint is met.  Now it's not clear here that the primary endpoint was actually met at all, because unblinding of the data might have taken place prior to choosing the primary endpoint analysis.  Nonetheless, we have the following reminder for when the endpoint is met.
		If, and only if, the primary endpoint is met pre-specified multiple secondary endpoints are tested as a family at an additional overall significance level.  Each endpoint in the family can use the .05 criterion for declaring significance, after its P value is adjusted for multiplicity.  For any secondary endpoints for which multiple testing issues were not considered a priori, statistical significance cannot be interpreted for regulatory considerations.  After performing the Hochberg procedure on four pre-specified major secondary endpoints with significance level of .05, the sponsor has exhausted their Type I error allotment for secondary endpoint.  No additional secondary endpoints can be declared statistically significant.
		Here I present the results from the four major secondary endpoints that you've seen before.  I present the estimated difference in mean change from baseline over time, CorCap minus control.  In the third column, I present the P values adjusted from an application of the Hochberg procedure.  As you can see from the table, only the P value for left ventricular end-diastolic volume, which is a structural endpoint, can be considered statistically significant according to the Hochberg procedure.  No other adjusted P value is less than .05, so no other secondary endpoint meets statistical significant.
		The focused cohort analysis must be prospectively validated with additional clinical data.  The sponsor has identified a subgroup that they claim benefits most from the CorCap, and excludes high-risk patients.  However, the sponsor has used the same data to choose the cohort, as well as to do statistical testing on the cohort.  This increases the risk of a finding that occurs purely by chance, because many subgroups were examined post hoc to find the one that gives the highest treatment effect.  I will briefly describe this analysis, and indicate why it cannot be used reliably as a stand-alone basis for approval of the CorCap.
		After examining a minimum of 19 covariates and their relationship with eight clinical outcomes,  the sponsor selected the subgroup that achieved the highest treatment minus control difference on the primary endpoint.  This subgroup they refer to as the focused cohort, and is the indicated population for which they're seeking approval.  		This is an example of one of 19 graphs, for 19 different baseline covariates for the clinical outcome mortality examined by the sponsor.  Each graph plots for each patient their baseline covariate value  by the cumulative treatment minus control difference on mortality up to that value of the baseline covariate.  The idea is to examine all 19 graphs, and choose a window, such as the one shown here, with the steepest positive slope, which corresponds to the greatest treatment difference in mortality.  This window then identifies the so-called focused cohort.
		The window chosen by the sponsor is shown here.  They found that when plotted against the covariate indexed left ventricular end-diastolic dimension, the cumulative difference in number of deaths between CorCap and control showed a steep positive slope between 30 and 40 units.  When they conducted the primary endpoint analysis using this subgroup, the unadjusted P value is 0.01.
		FDA has concerns with the analysis of the focused cohort.  Choosing a focused cohort based on cumulative trends analysis, such as what the sponsor did, is equivalent to choosing a best subgroup based on P values from the primary analysis.  This is because the treatment minus control difference is maximized.  Essentially, a hypothesis was chosen using data that was later used to test the hypothesis.  For the sponsor's analysis, many subgroups were examined prior to choosing the best.  This increases the risk of a Type I error.  
		To show how easy it is to obtain a Type I error using the sponsor's chosen analysis, I tried the analysis using simulated data consistent with a true null hypothesis of no treatment effect.  I simulated 300 binary outcomes from a distribution with failure rate of 40 percent, and randomly assigned the outcomes in a 1 to 1 ratio to two groups, say treatment and control, so the null hypothesis of no treatment difference is true here.  Then I simulated 19 independent covariates from a standard normal distribution for each simulated patient.  These 19 graphs are from the 19 independent covariates, consistent with how the sponsor's cumulative trend analysis is carried out.  However, look at the plot for covariate 18, which is expanded in the next slide.
		If you choose the covariate range where the slope is steepest, and conduct a two-sample test for equality of proportions, we get a Type I error, because we would reject a true null hypothesis with a P value of .028.  This demonstration shows that the method by which the sponsor chose their focused cohort could have easily led to a Type I error.  Therefore, the supposed statistically significant results from the focused cohort analysis capitalized too much on chance, and cannot be used to reliably support approval of the device.
		In summary, there was a large amount of missing data in the primary endpoint due to the sponsor's decision to enroll patients prior to agreement on the primary endpoint.  Sponsor's agreement to use imputation appeared to come after the data were unblinded.  Examination of separate components of the composite shows a strong influence of reduction in major cardiac procedures, additional major cardiac procedures for the CorCap group.  There was no difference in mortality between the CorCap and control group at the common closing date.  And there was no significant difference in change in NYHA.
		The results for a major secondary analyses found statistically significant CorCap benefit for structural, but not functional endpoints.  Finally, results from the post hoc analysis of the focused cohort are good for offering some insights into future studies, but not sufficient to provide valid scientific evidence to support device approval.
		I would now like to introduce Dr. Clyde Yancy, one of the primary reviewers from the June 2005 Advisory Panel meeting.  Dr. Yancy also participated fully in FDA's post panel review as a consultant to ODE.
		DR. RAMSEY:  As just as a reminder, we're at about 30 minutes.
		DR. YANCY:  Good morning, and thank you for the opportunity to address this panel.  My name is Clyde Yancy.  I am Medical Director of the Baylor Heart and Vascular Institute in Dallas, Texas, and Chief of Cardiothoracic Surgery at the same institution.  My relevant disclosures are displayed on this slide.  I did receive support for travel and housing, but no other resources.
		I am pleased to be able to address this Dispute Resolution Panel, as I was a member of the original FDA panel that reviewed the PMA for CorCap, and served as one of the lead reviewers for these data.  Given that you're being asked to review fundamentally the same data set, I would like to provide context for our past decision, and highlight our residual questions.
		Let me be clear.  This is neither an easy process, nor easy proceedings.  Many of us in this room are one and the same.  As investigators, we align ourselves with new concepts and sponsors, and work together to test new drugs, devices, and paradigms.  As reviewers, we accept the responsibility to offer unbiased and objective assessments of new data that may influence the health of patients.  And as clinicians, we respect the highest order to help as many patients as possible, while taking every precaution to do no harm.  Today, I wear the cap of a previous reviewer, but I understand the issues of the investigators, and the responsibility of this panel.
		Given the burden of heart failure, the availability of effective adjunctive therapies that modify the natural history of this disease remains desirable.  The target of recent drug and device therapies has been to generate favorable changes in left ventricular structure and function.  A reduction in left ventricular size, improvement in left ventricular ejection fraction, and change in geometry to a more elliptical shape are hallmarks of effective heart failure therapies, and collectively, this response is known as reverse remodeling.  The technology we are reviewing today is hypothesized, as previously stated, to effect similar changes to the left ventricle.  
		The investigators, quite frankly, are to be commended for investigating an ill patient population who has an unmet need for more effective treatment options, and to do so with novel device technology that tests the benefits of surgically induced reverse remodeling of the failed left ventricle.  As highlighted by Lawrence Cohn in a recent editorial in the Journal of Thoracic and Cardiovascular Surgery, there is, in fact, a critical need for more evidence-based data in cardiac surgery.  And investigators have met that challenge, and should be acknowledged for incorporating a prospective evaluation of mitral valve repair.  Recent publications by Dr. Acker, who is with us today, have demonstrated convincingly that MVR in the setting of advanced heart failure is of benefit.  Dr. Bolling's work supports that.  Clearly, they have demonstrated that a meaningful clinical trial can be done in the device surgical setting when the hypothesis is valid, and methodology is sound, and the procedure can be done safely.  Large numbers of patients are not needed.
		The fundamental question we now face is whether surgically induced reverse remodeling achieved with the CorCap results in similar efficacy as medically mediated reverse remodeling.  A device is not a drug, and reducing ventricular size is not equivalent to reverse remodeling, and is insufficient to establish evidence of clinical benefit.  Primary data are required to be certain regarding efficacy, clinical effectiveness, and the safety of surgical reverse remodeling.  		The events of last week in this very room with a specially convened FDA panel to evaluate post hoc experiences with another cardiovascular device represent a Lesson Learned.  The adequacy of data in the PMA needs to meet a higher bar than in past experiences.  The intent of these investigations was to demonstrate that application of the CorCap to patients with Class III and IV heart failure, who were already on standard medical therapies, were resulting in improvement in the composite that has been explained multiple times.  That composite endpoint yielded a P value of less than 0.05. 
		However, the available data did not yield a positive result on mortality, as expected, given that the study was not powered to detect such.  The assessment of NYHA class was not interpretable, as it was confounded by critical data entries, perhaps as much as 50 percent; thus, necessitating an imputational analysis.  And, finally, despite a benefit on major cardiac procedures, especially heart transplant referral, one must acknowledge that this was an unblinded trial, and the investigators were aware of the endpoint composition.  Unintended referral bias is a concern, and was a concern of the original panel.
		Notably, the results in composite endpoint was highly dependent upon the imputational data regarding NYHA classification.  You've heard the statistical debate today regarding the appropriateness of any imputational analysis given the degree or missingness, the correct methodology to be used, and the resulting interpretation.  As you've seen, a separate FDA analysis using actual NYHA data only, without imputation, yielded a composite P value greater than 0.05.  We are here today in large measure due to use of an imputational analysis for NYHA status.
		From a pragmatic approach, and as the stewards of the public trust regarding the application of new drugs and devices, the fundamental question to be answered is whether or not this cardiac restraint system has met the bar required to be incorporated as safe and effective treatment strategy for patients with advanced heart failure.  We must briefly address several questions to fully adjudicate this treatment modality.  What was the rationale, what was the premise, and is that premise supported by these data?  What were the issues that impacted the original panel, and how would this panel and the original panel write a label if this technology is approved?  
		What was the rationale?  The rationale, simply put, that patients with Class III or IV heart failure have limited effective treatment modalities.  But as you can see from these data, that may no longer be the full case.  Note, while the ACE inhibitors have been shown to reduce mortality, beta blockers are effective in patients with very low ejection fractions, aldosterone antagonists reduce mortality in patients with advanced disease who have been recently hospitalized, cardiac re-synchronization therapy improves outcomes for advanced heart failure, including ambulatory Class IV.  There are even recent data to suggest that a selected Beta II agonist may provoke dramatic reverse remodeling in patients with a dilated cardiomyopathy, who require mechanical support, and especially for patients with advanced heart failure, referral to a sophisticated disease management program represents a Class I recommendation.  We must determine, then, in the current context, is there a benefit of the CorCap beyond these already proven or suggested therapies?  
		What was the premise?  In a statement from the CorCap cardiac support device expert consultant opinion memorandum, the following statement appears:  "Because dilation, and not contractile dysfunction, appears to be responsible for the severity of disease, the mitigation or prevention of the dilatorious dilation process is an important therapeutic endpoint for patients with this life-threatening therapy.  Therapy that specifically targets remodeling offers an important step in the treatment of heart failure.  It is widely accepted that reverse remodeling of the failing left ventricle is associated with an improvement in clinical outcomes.  I support the statement made by the CorCap expert consultation panel.  Indeed, reverse remodeling has the potential to represent a surrogate marker of mortality benefit in heart failure trials.  However, the work of Burkoff and others has raised the question, the surgical approaches that purport to reconfigure the left ventricle may, indeed, reduce left ventricular size and improve systolic function, but not impact reverse remodeling, as diastolic function may be impaired and/or compliance worsened."
		On this next slide are data from the work of Burkhoff.  With a surgical reduction in left ventricular size, there's a shift to the left of both left ventricular end-systolic and end-diastolic pressure volume relationships, but the shift in left ventricular end-diastolic pressure volume relationship is greater, resulting in a stiffer, less compliant ventricle.  Note this demonstration in Panel B.
		This potentially adverse physiologic response has been implicated for several surgical approaches that target reverse remodeling.  Admittedly, it has not been established for the CorCap, but data from the current study do demonstrate that the impact on LV diastolic volumes and LV diastolic dimensions is greater than the effect on LV systolic parameters; and, thus, the question is raised that diastolic function may be negatively impacted by this technology.
		It is acknowledged that colleagues have done impressive seminal work to demonstrate important improvements in cell signaling consistent with the reverse remodeling effect of the CorCap, but these are animal data that may or may not reflect a likely clinical scenario.
		Additional questions are raised, even more so, after the consideration of the uncertain effect of long-term fibrosis of the mesh enclosure, and how that might impact ventricular compliance and diastolic function over time.  Those data are not known, and were of concern to the original panel.
		There are, admittedly, data to support the concept that surgical reductions in LV size results in favorable clinical outcomes, but this paradigm appears to be most relevant for the ischemic substrate in the patients we're looking at today, for the non-ischemic substrate primarily.  Surgical reverse remodeling may work best by removal of akinetic or dyskinetic myocardium, but this remains a question.  And, in fact, there's an ongoing NIH trial to definitively address this issue, so it remains an unproven concept.
		What were the issues that impacted the original panel?  The primary composite of mortality, NYHA function class, and need for major cardiac procedures was achieved with a P value, as noted.  Yet, there was no demonstrable effect on LVF, despite a decrease in LV size, minimal changes in objective measures of functional capacity, and no change in the BNPS, the strikingly low BNP value noted for a patient population with advanced heart failure.  The lack of consistency in these components and the inconsistent results seen in the secondary objectives, as previously reviewed, raise questions about the data supporting this application.
		Again, consider that one of the components of the composite endpoint, NYHA classification, has significant data elements missing; and, as well, the site-based versus core lab based assessments differed.  The amount of missing data, whether acceptable or not from a statistical basis, and we've heard the arguments today, unfortunately generates reasonable clinical doubt, and raises questions even more so.  Are we as clinicians in clinical trials comfortable with an endpoint for which nearly 50 percent of data elements are missing, and the contribution of that endpoint to the overall primary endpoint analysis is a different between P less than or greater than 0.05?
		How would this panel, or the original panel write a label if this technology is approved?  CorCap would be applied as adjunctive therapy for advanced heart failure in patients with a non-ischemic ideology of heart failure, already on reasonable medical therapy, were acceptable candidates, in part, based on the focused cohort analysis.  Application of the device is expected to yield a reduction in a combined endpoint of the risk of death, need for major cardiac procedures, and quality of life.  
		I would ask this panel, is the foregoing label justified?  Do the data support comments regarding reduction of risk of death?  Are the data convincing that quality of life is improved?  Do we know which patients respond best, those with concomitant mitral valve surgery, those without concomitant mitral valve surgery?  Even the very provocative focused cohort analysis seen by this reviewer, but not by the original panel, does, in fact, suggest a population in whom the benefit of the CorCap might, indeed, be realized.  But, as has been stated, this represents a hypothesis only, and must be tested prospectively.  
		It is difficult to interpret lesser need for CRT, when the current indication for CRT is established by the presence of Class III heart failure and optimal therapy, with care as per longation.  Would a patient opt for a surgical intervention instead of CRT, a per cutaneous procedure?  An important question was, was the need for transplantation surely reduced, or simply the referral for transplantation reduced?  These are the questions that impacted the original panel.  
		In conclusion then, given the availability of alternative effective treatment options, a hypothesis that has not yet been proven, and may, perhaps, be disproved, data that are clearly provocative and encouraging, but remain with questions, and difficulty with clarity in labeling language, one must surmise that more data should be acquired prior to proceeding forward with unlimited availability of this technology.
		This is not bad technology.  It's certainly not faulty investigators, and the sponsor is, indeed, sincere and appropriate.  The answer here really should not be yes or no, but how should this technology move forward; as an unlimited approved indication, or as a promising ongoing intervention still under investigation with provocative preliminary data worth pursuing.  This was the opinion of the original panel.
		In the absence of desperate circumstances, we, as physicians, investigators, and the regulatory body who are considering novel technologies, we should be of one mind and follow an iterative process of hypothesis generation, data acquisition, and demonstration of clinical efficacy, and effectiveness.  It is the consistent view of the original panel that questions remain, and that, regrettably, the original decision remains relevant.
		I will now turn the podium back over to Ron Yustein.
		MR. WEINSTEIN:  I'd like to clarify that Dr. Yancy is here today as a consultant to the Office of Device Evaluation, and not as a member of the Circulatory Devices Panel.  
		DR. YUSTEIN:  Thank you, Dr. Yancy.  In summary, as you have heard, there have been extensive interactions between the sponsor and FDA throughout the entire IDE and PMA process.  FDA believes that the sponsor has worked diligently to provide available data and expert analysis.  Likewise, ODE and the Division of Biostatistics have reviewed all of the data presented by the sponsor fairly and objectively.  During the course of our review, we have applied substantial internal and external resources, and expertise to this project in an effort to fully understand the data submitted.  Unfortunately, as you have heard, FDA continues to have several significant concerns regarding the clinical data and its interpretation.
		In conclusion, I would like to revisit and summarize these main concerns with the Acorn CorCap clinical trial data one last time.  Number one, as discussed, for a variety of reasons, the primary composite endpoint result is not interpretable.  Number two, the objective secondary endpoint results are problematic, and not supportive of trial success.  Number three, the safety concerns raised by FDA and the original June 2005 Advisory Panel have not been adequately addressed by data provided from this study to provide a reasonable assurance of safety.  Number four, pre-specified subgroup analysis of the MVR, and no-MVR strata do not indicate that there is a subgroup where the risk benefit profile of the CorCap device is optimized in relation to the 300-patient cohort.  And, finally, number five, the focused cohort analysis, which is the indications for use being sought by the sponsor, may have identified a target population which the risk benefit profile of the device is optimized.  However, FDA strongly believes that the results of this post hoc analysis for reasons cited during our presentations, do not constitute valid scientific evidence that the CorCap is safe and effective.  In order to support device approval, FDA believes that these results must be prospectively validated in an additional pre-market clinical trial.
		For these reasons, ODE does not believe that the sponsor has provided sufficient valid scientific evidence that demonstrates a reasonable assurance of safety and effectiveness for the CorCap for its intended use.  Therefore, we continue to recommend that the Acorn CorCap CSD application be found not-approvable at this time.  FDA does not believe that any proposed post approval study alone can substitute for the need to provide a reasonable assurance of safety and effectiveness prior to approval, and we welcome the opportunity to work interactively with the sponsor to design an additional pre-market confirmatory study to validate the focused cohort results.  
		That concludes FDA's presentation for the Acorn CorCap device.  Our reviewers and expert consultants will be available throughout the day in your deliberations to answer any questions you may have.  Thank you for your time.
		DR. RAMSEY:  And thank you very much for a timely presentation.  So we have some time now for, again, clarifying questions from the panel to the FDA.
		DR. SACKNER-BERNSTEIN:  I note that the technique of multiple imputation was first suggested by ODE, it sounds like from the documents.  I'm wondering if anyone from the agency can confirm whether this has been the technique for which there is a precedent in device approval process?
		DR. RAMSEY:  Please identify yourself.
		DR. CAMPBELL:  Yes.  I'm Greg Campbell. I'm the Director of Biostatistics in the Office of Surveillance and Biometrics at the FDA.  There have been other instances where people -- where imputation has been used as part of an application to the FDA, but probably not as the main primary analysis within the Center for Devices and Radiological Health.
		DR. SACKNER-BERNSTEIN:  I'm sorry, so it probably hasn't been used, or it has been used?  I don't mean to be a stickler, but just -- 
		DR. CAMPBELL:  I think it's fair to say that imputation has been used in the past, but not as the primary prospectively agreed upon mode of analysis.
		DR. RAMSEY:  On that note, if it's possible, this may not be possible, can the FDA give us a sense of how much missing data is common in a device trial of this type, or is that just beyond - because you have seen one trial, you've seen one trial.
		DR. ZUCKERMAN:  Dr. Zuckerman.  I've been with the Division of Cardiovascular Devices for the last 10 years.  I can state that in my experience, we generally have seen in PMA pivotal trial, pivotal cardiovascular device trials, 20 percent or less missing data.
		DR. SACKNER-BERNSTEIN:  And when you give that figure, you're comparing that to which figure that you would apply to this data set using a common definition, because we've heard a lot of different definitions about how much is missing here.  Dr. Zuckerman.
		DR. ZUCKERMAN:  This is a complex situation, and the ability to give an absolute number is an extremely difficult one.  I think the essence that we try to propose to the sponsor, and which is captured in our response letter in Attachment 21 to Supplement 45, is that we were in a difficult situation with the sponsor.  Hence, we suggested that the sponsor utilize a set of analyses, and approach this data set looking at the combined analyses and the totality of the data  without a single reliance on one particular analysis.  And that's what's captured, I believe, in Attachment 21.
		DR. RAMSEY:  Any other clarifying questions from the panel?
		DR. DeMETS:  I have a question that probably could be best answered by the sponsor, so I don't know if we're breaking protocol, but the question has - maybe the FDA can answer it, too.  I'd like to hear more about the New York Heart classification by the core lab.  I haven't heard much about that, and I'm not sure I understand how that was done.
		DR. RAMSEY:  I've been advised that we should wait on questions for the sponsor until the question and answer period between both, so if you don't mind.  Okay.  At the end of the rebuttal period, we can have some more of those questions.  Any other questions for the FDA?
		DR. LASKEY:  Maybe a partial question for the sponsor, but one for the FDA, as well.  In Dr. Becker's presentation, Item 6 in her last slide says focused cohort is post hoc, and not necessary for approval.  Where is the agency's position on should we or should we not discuss the focused group later today?
		DR. ZUCKERMAN:  Okay.  Thank you, Dr. Laskey, for pointing out that fundamental disagreement between the sponsor and the agency. I think there are several things to consider.  Again, I would propose that you ask the sponsor correctly, but I think why Dr. Becker made that statement is that they've concluded that the original trial result could stand on its own as a positive trial, and they just utilized the focused cohort analysis to identify a focused patient population with a more optimal risk benefit profile. 
		The agency, on the other hand, has a fundamental disagreement here.  We do not believe that the original 300-patient trial can stand on its own.  We, therefore, look at the focused cohort analysis, as Dr. Thompson elaborated, and can elaborate in more detail this afternoon, as an interesting subgroup analysis.  If prospectively validated, it might be very applicable for approval of this device with the current indication.  The current indication is not the indication that was originally in the 300-patient trial, but is the focused cohort analysis indication.  That's why, as Dr. Yancy indicated, we're in this black box area where we think the appropriate measure is just to get the appropriate data to answer the question definitively.
		DR. RAMSEY:  Any other questions from the panel?  It might be worthwhile that when we return to the rebuttal section, to have Acorn comment on whether  they're seeking approval specifically for the focused cohort, or for the entire cohort.  I think I know the answer, but I think there is also a little bit of confusion, so if that doesn't take much time, we'd appreciate it.  Do you have another question? Okay.
		DR. SACKNER-BERNSTEIN:  One question to Dr. Pina, just to make sure I understand correctly, some of the data you presented about the functional assessment six-minute walk, and VO2 max.  This sponsor has presented an analysis of each of those parameters that suggests, at the minimum, a numerical advantage in favor of treatment.  And you've shown data that shows at minimum a numerical advantage in favor of control.  My interpretation of those two is that you used available data, and they used one of several analyses that could have included worst rank.  I think when I look at the protocol that the primary specified analysis was data that was available.  Is that your understanding, too?
		DR. PINA:  Yes, it is.  That's my understanding, and I need to say that the exercise tests that were done were extremely well done, and the analysis of those tests were extremely well done.  But yes, what I showed was available data.  Dr. Zuckerman, do you want to respond?
		DR. ZUCKERMAN:  Perhaps Dr. Sackner-Bernstein would also like Dr. Thompson to comment on the limitations of the statistical analysis that the sponsor has performed with those available data.
		DR. THOMPSON:  Thank you, Dr. Zuckerman.  Regarding the analysis the sponsor presented with the estimated odds ratios that showed favoring CorCap, we have several problems with that analysis.  Next slide, please.  First, the ranking categories that were chosen for that odds ratio calculation were chosen post hoc, not prospectively.  Second, a rank provides less information than an original value.  The prospectively planned analysis that were presented by  Dr. Pina used original values, continuous values.  Third, the rank analysis does not deal adequately with missing data.  Patients with missing data were mostly ranked as did not attend visit, and that doesn't appear to be helpful with regard to their actual value on one of the exercise tests.  Thank you.
		DR. RAMSEY:  Any further questions?  If not, we will break for lunch.  We're about five minutes ahead of schedule, and I'd like to keep to that, if possible, just in case we need a little more time for discussion, so we will come back at 12:40.  And I'd ask you to leave as soon as you can from the room, because we have to secure the room during the break.  You may want to take your personal belongings.  We'll see you back at 12:40.
(Whereupon, the proceedings went off the record at 11:55:25 a.m., and went back on the record at 12:45:45 p.m.)
		DR. RAMSEY:  Let's go ahead and get started.  I know that Nancy Braier is working on loading a presentation, but I think in the interest of time and timeliness, if both parties don't mind, we'd like to go ahead and get started.  So I will now reconvene the panel, and call us back to order.  And at this point, Acorn has 15 minutes to follow-up, to present their rebuttal to the FDA, or present any other clarifying information that they would like.  At the end of that, we'll have a very brief session where the panel can ask another set of clarifying questions to Acorn before the FDA has their rebuttal.  So if you're ready, Acorn, you're free to start.
		DR. BECKER:  Thank you, Dr. Ramsey.  I want to just make a clarification to the question about is the sponsor - did we speak correctly when we said that we feel the original cohort supports approval of the product.  And I think Dr. Zuckerman explained it very well, and the answer to that is yes, we do feel that the original cohort provides valid scientific evidence to support approval for the product.  And that the post hoc analysis is exploratory, and is not sufficient to establish safety and effectiveness on its own.  
		I do want to just clarify a couple of things.  One is, we are absolutely not disparaging the work of the previous panel in any way.  They raised many important questions, and that's the reason why the PMA was amended.  And you have additional information before you today that they didn't have to clarify the very questions that they raised.
		Also, the PMA was amended to include that focused cohort analysis at the suggestion of FDA, as one of three possible ways to put the PMA into approvable form.  In that letter, FDA warned the sponsor that this may not be statistically valid.  And, as you can see, I think that we are all in agreement that if it were to stand on its own, it would not support an approval.  However, we do feel quite comfortable that the original cohort did establish safety and effectiveness.
		Now as to the labeling, the label in the amended PMA does include a revision to the label that Acorn felt it would be conservative for the purposes of safety to reduce the indication for use based on ventricular size.  However, we are absolutely open to any discussion or considerations that the panel may deem to be appropriate in terms of a proper label for this device based on the data available.  You know from your work with other products that when we write a label for a product, we don't always pick up the inclusion and exclusion criteria that we've used in the clinical study.  We use all the information we have available to us, sometimes many studies, in order to prepare a proper label.
		DR. PIANTADOSI:  Thank you, Dr. Ramsey.  I'm  Steve Piantadosi.  I'm going to lead or begin the discussion of the rebuttal, or the remaining points of the rebuttal from the sponsor.  To do so, I need to return to a slide I showed you this morning, which contains a listing of the types of pitfalls that are potentially misleading here.  And let me begin with the first one, wherein I said that an overly strict adherence to P values as a measure of evidence was potentially misleading.  And to see that, I'll show you one of the FDA's own slides, that contains a series of analyses that they proposed.  The first is not especially in dispute.  It's the imputed analysis that the sponsor has put forward.  The other three analyses, FDA has quite correctly had pointed out, have certain flaws, not the least of which in the second one is a discarding of a significant fraction of the information, wherein NYHA is missing.  And they've highlighted the lack of significance of some of these analyses.  But this display contains something more important than inconsistency in the P values.  It contains the same relative odds ratio for all of the analyses.  And the reason for that is because there is a treatment effect.  And the fact that the P values are not significant is more a reflection of lack of precision or sample size, than it is any fundamental biological inconsistency.  
		There are some similar types of sensitivity analyses that the FDA did not show, and they're on the next slide.  There they are.  And the ones with asterisks are protocol-specified analyses that were not shown, and then there are some others based on imputation.  Time won't allow me to go into all of the details here, except I will mention that this blinded third-party multiple imputation is the one that Dr. Rubin discussed in some detail with a similar significant odds ratio to that which was presented on the previous slide.
		The point here, again, is that the odds ratios for all of these sensitivity analyses are giving us the same message, so in a sense, it's somewhat irrelevant about how you nuance the type of analysis.  The modest connection between site-assessed and central-assessed NYHA is irrelevant, because no matter how you resolve that question, you get the same treatment effect.  The only thing at play is the exact level of statistical significance.
		Let me go to the second bullet, taking subgroup findings as primary and definitive.  This is a mistake, as we all know.  The focused cohort, for example, is one such subgroup.  The FDA has explained very eloquently the limitations of that subgroup analysis.  We should also understand the limitations of subgroups defined by the individual treatment strata, and I'll return to that point in a moment.
		Third, deconstruction of the primary outcome.  FDA, for example, used this in, what I would consider to be a very aggressive manner in saying that we should look for the signature of remodeling in the survival outcome.  Survival is not, necessarily, a surrogate for remodeling measures, so deconstructing the primary outcome and teasing out the survival piece from that, and saying that it must show the effect of remodeling is really not a valid argument.  We have remodeling measures.  If you want to look for the effect of remodeling, look at the data based on remodeling measurements, and you'll see significant differences there.
		Next bullet, misunderstanding the role of stratification.  As I indicated, this is partly a subset issue.  Within strata analysis were not pre-planned in the protocol.  The protocol called for a pooled analysis across strata.  Now what the stratified randomization does allow is a valid estimate of the treatment effect, the odds ratio within the strata, but it does not guarantee that you'll expect to see a statistically significant effect within strata.  And as we showed repeatedly through the morning, if you look within strata at the odds ratio, you see the same treatment effect as you see overall.
		And then, finally, misinterpretation of the potential effects of missing data.  This explains several findings in dispute here.  The first point that the panel needs to understand is that the available data are subject to informative missingness; that is, analyzing only the available data in the raw form, ignores the fact that some of the data are missing because patients were doing poorly, and they did not return for rescheduled tests.  I know that a couple of the panel members are familiar with the National Emphysema Treatment Trial.  We had exactly the same problem there, and we classified our functional outcomes as several levels or degrees of improvement, and we classified individuals who did not return for their functional assessment, or died, as unimproved.  That is conceptually no different than what's been done here.  So if you analyze only the available data, informative missingness will show you a treatment effect in one direction.  The sponsor's analysis has tried to recover that missingness by classifying the patients who were apparently too sick to return as being unimproved, and that allows us to use that information, and get a more correct estimate of the treatment effect.  So we can't be dependent on discarding incomplete data, it violates the intention to treat principle.  We have to find some way to recover that complete information; otherwise, we can't honor the very valid principle of intention to treat.
		I think I'll close my remarks there, and Dr. Mann, I believe, will offer some additional perspective in our time.
		DR. MANN:  Thank you.  With the remaining time, what I'd like to do is address the question of whether the CorCap does, indeed, lead to true reverse remodeling.  I think both the FDA clinical consultants and the Steering Committee on the Acorn trial both agree on the importance of cardiac remodeling, or reverse remodeling, as a valid biologic surrogate for an effective therapy that leads to myocardial recovery.
		I think there were two arguments that were raised that I'd like to directly address, the first of which is that we didn't show mortality benefit and beta blockers do show mortality benefit.  Both therapies lead to reverse remodeling; however, I would like to remind the panel that it takes about 3,000 patients to show a mortality benefit in the beta blocker trial, we only had 300 in the Acorn trial, so I wouldn't have anticipated mortality benefit, even though there was reverse remodeling.
		The second argument that was raised, this is an acute surgical intervention that leads to a shrinkage of the heart.  And I think that the comparison to the SAVER procedure or the DOR procedure is a bit specious, because as I'll show on this slide, this leads to physiological unloading of the heart, and time dependent changes in the ventricle that are accompanied by a molecular signature of reverse remodeling; namely, a decrease in myocyte size, and a reversal of the fetal gene program.  As shown here, the CorCap CSD actually applies general external pressure to the heart of about two millimeters of Mercury.  What this does is, it actually leads to a decrease in transmural pressure of the heart, and that's shown here.  Normally, the left ventricular end-diastolic pressure is 20, if then you have a plus 2 millimeter Mercury pressure on the outside of the heart, what it does is to lead to a decrease in the transmural pressure, which actually decreases the wall stress of the ventricle, so this actually physiologically unloads the ventricle.
		Now if this did cause constraint, one would expect to see a shift upward and to the left of the pressure volume curves.  We're actually fortunate to have actual data in humans done with micromolar catheters for patients who underwent the CorCap procedure.  These are the pressure volume curves at baseline, and you can see that the pressure volume curves shift downward and to the left in the patients who had the CorCap procedure placed.  And this is consistent over time, so it's consistent at three, six, and twelve months.  If this cause constriction, such as the SAVER procedure does, or if it caused pericardial constriction, what one would see is that the pressure volume curve shift upward and to the left, and that clearly doesn't happen.  Furthermore, these data are identical to what has been reported in  JACC by David Kass and Tony Seebach in the animal models.  So, in summary, there's really no evidence at all that this causes constriction.  It's not at all like the SAVER procedure or the DOR procedure, and, in fact, is entirely consistent with what we see with beta blockers and bi-ventricular pacing.  Thank you.
		DR. BECKER:  Thanks.  We just have two more slides.  I believe it was Dr. Sackner-Bernstein asked the question, to what extent is data missing in other trials, and we have two slides to show you some examples.  This is the percent of missing data in other heart failure device trials for this endpoint echo cardiography, and you see the Miracle trial, Miracle ICD, and the Acorn trial.  And in terms of all of these endpoints, you see that in the Acorn trial the amount of missing data is less than what was seen in most studies.  The next one.
		This is another example for another endpoint cardiopulmonary exercise testing, and you see that previous device studies also have significant amounts of missing data in some of these endpoints, Miracle Contact CD and the Miracle ICD, and that's Acorn down at the bottom, all pretty much within the same range.  Okay?  And that concludes our rebuttal.  Thank you.
		DR. RAMSEY:  Thank you very much, excellent.  Now it is time for the FDA to have their follow-up or rebuttal, and they, like Acorn, have 15 minutes.  But first, before we do that, we do have one - just a couple of moments if anyone from the panel has any clarifying questions for Acorn regarding their rebuttal.
		DR. SACKNER-BERNSTEIN:  Can I ask a question in general about their presentations, or just what they discussed during the rebuttal?
		DR. RAMSEY:  I think you could ask anything that's relevant, sure.
		DR. SACKNER-BERNSTEIN:  Okay.  First of all, did you get a chance to see whether you had the data on the difference in the frequency of wide QRS complexes in the groups at baseline?
		DR. MANN:  This is Doug Mann.  With permission, I have the data from Acorn.  If you'd like, I can distribute it to the panel members.
		DR. RAMSEY:  Sure.
		DR. ZUCKERMAN:  Could we obtain a copy too, please?
		DR. RAMSEY:  Yes, if you wouldn't mind giving one to FDA, as well.  
		DR. SACKNER-BERNSTEIN:  Do you have data on how frequently people have wide QRS at baseline in the different groups?  I'm trying to get at whether there's a difference at the beginning perhaps by chance, but in just a 300-patient trial perhaps there were a much larger proportion of patients who had wide QRS in the control group; and, therefore, many more opportunities to think about a Bi-V pacer over the course of the trial.
		DR. MANN:  I'm sorry.  At this time, we don't have those data.  We will try to find them at baseline.
		DR. RAMSEY:  Any further questions from the panel?  Yes, please.
		DR. DeMETS:  I asked earlier about a little further explanation on the New York Heart core lab, could you tell us more about that?  We have not heard anything about that.
		DR. BECKER:  We are prepared to have Dr. Spencer Kubo do that now, if you would like.
		DR. RAMSEY:  I think we need to have the FDA give their rebuttal, and perhaps you can present that during the question and answer session, because I expect we'll still want to hear about it at that point.  Any other clarifying questions, and then I'll turn it over.
		DR. CRITTENDEN:  The missing data that was discussed just a few slides ago, did that involve the primary endpoints for these studies, or are they the secondary endpoints?
		DR. MANN:  Those were secondary endpoints, and some were in the primary four endpoints and some were not.  The exercise data were outside.
		DR. RAMSEY:  Okay.  Oh, sorry, one more.
		DR. SACKNER-BERNSTEIN:  I'm curious if I could hear an explanation from Acorn as to who was involved with the decision to change stance on the use of imputation?  Where did that decision come from within the corporation?
		DR. BECKER:  We can have Steve Anderson answer that question for you.
		MR. ANDERSON:  Good afternoon, I'm Steve Anderson. I am the Regulatory Officer for Acorn Cardiovascular.  On May 19th of 2004, we were, as Dr. Zuckerman talked about before, nearing the close of the trial, and we received a letter from the FDA that changed the stance from our March meeting, in which they had told us don't make any changes.  And to FDA's credit, their suggestion was a good one, but they said do not use unblinded assessment within your primary endpoint, which is site NYHA, don't combine the two instruments; rather, we suggest imputation.  
		Now we had a small number of individuals scheduled to unblind on June 1st, as a small company, for the purposes of fund-raising.  We had to raise funds in the fall to get the small company through the PMA process.  We had to have some idea during that process if, indeed, we were even remotely close on the study.  So what we did at that point is, we had a few days to make a decision.  We briefly investigated it, had some initial input from some certain statisticians who were not imputation experts, unfortunately.  They said we're not certain about this, and the clinicians were uncertain about it.  It's an esoteric topic, so we told the FDA in our letter, we said we'd prefer to keep, as you told us in March, the site to core analysis.  However, we would do it as an additional analysis, and we'd also like, if you could, for the question we've had before, give us some additional information from the FDA on the use of imputation.
		Then what I did is, as a Regulatory Officer, realizing that this question was still hanging out there and we needed to get this resolved, we specifically kept our Director of Regulatory Affairs  blinded to this process and her staff.  They were kept blinded from all results, and over the next couple of months, they investigated very thoroughly with statisticians and imputation experts regarding simple methodology; is it or isn't something that actually makes sense, and does it make more sense than what we're already doing. 
		Towards the end of July, while still blinded, this statistical expert came back and recommended to us that imputation was, indeed, the most appropriate methodology, and the most scientific use and way to account for the missing data.  Our Director of Regulatory Affairs then on August 6th, while still blinded, sent in a letter to the FDA saying we have made a decision.  We've agreed to impute, per your recommendation in the May 19th letter, so including the model parameters that they had recommended, and we received a phone call from Mike Burman, the reviewer, noting on August 15th that they had received this, that they understood it, and he said we won't be sending you a new letter, because you already had an unconditional approval.  So that was the basis behind it.  We knew that we had to set up mechanisms to protect the sanctity of the data, and we did that within our organization.
		And I also would like to add that over the course of the PMA review, the filing of the PMA, the initial review, the Advisory Panel, and the two not-approvable letters, and a negotiation of the Ombudsman's issues, this idea that we had somehow violated the sanctity of this has never before come up.  We only learned about this issue one month ago during the exchange of the panel packs, so it was quite a surprise to us that this was an issue.  And, in addition, we've never ever been asked a question before during two years of dealing with this issue.
		DR. RAMSEY:  Thank you. Well, I think we should move on and have the FDA present its rebuttal at this point.
		DR. HILLEBRENNER:  Hello.  My name is Matt Hillebrenner.  I am a Bioclinical Engineer in the Division of Cardiovascular Devices, and the lead reviewer for the Acorn CorCap PMA submission.  I want to thank Dr. Ramsey and the other panelists for your time today.
		Before we move into the open panel discussion this afternoon, I would like to offer a few thoughts on behalf of the FDA review team.  We have a lot of statistical expertise in the room today, Drs.  Rubin and Piantadosi on my left, Dr. DeMets and colleagues on the Dispute Resolution Panel, as well as Drs. Thompson and Campbell from the FDA.  There is always a danger of becoming P value centric, and losing sight of the data when in the presence of such esteemed individuals; thus, I think it is important that we remember the dispute under discussion today involves not only P values, and the intricacies of imputational methodology, but more important, the relevance of the data.  We are also not here to debate the actions of the sponsor or FDA throughout the review process.
		This scientific dispute is fundamentally about interpretation of clinical evidence.  At the end of the day, the following clinical questions need to be answered in a definitive way.  Do the overall treatment results, as well as the observed treatment differences in the MVR stratum justify placement of the CorCap concomitant with mitral valve surgery?  And do the overall treatment results, as well as the observed treatment differences in the no-MVR stratum justify performing a median sternotomy solely for the purpose of placing the CorCap device?  To both of these questions, the FDA answers no, due to several concerns. 
		You have heard FDA indicate that the primary composite endpoint is difficult to interpret.  For example, there are questions regarding the lack of validation for the core lab NYHA assessment due to poor correlation with other standard markers of severity in heart failure.  In addition, the fact that a greater percentage of patients in the control group, as compared to the treatment group, improved in site NYHA, makes it unclear what an improvement in core lab NYHA means from a clinical, rather than statistical, perspective.  In addition, Dr. Pina's breakdown of the major cardiac procedure results raises practical concerns about referral bias in this unblinded trial.
		The bottom line is that FDA is left with many unanswered questions regarding clinical interpretation of the primary endpoint.  We then proceed to the secondary endpoint results.  Let us put Benjamini Hochberg aside for a moment, and focus on the clinical relevance of the available data.  Do we want to perform a median sternotomy and place a foreign material wrap around the heart for a treatment difference in ejection fraction of less than 1 percent, a Minnesota Living with Heart Failure change of fewer than 5 points, and a lack of benefit in exercise-testing endpoints in a predominantly Class III heart failure population?  The FDA suggests that the answer is no.
		The sponsor purports that there is a rich clinical trials database suggesting that a reduction in left ventricular dimensions is associated with important decreases in mortality and hospitalizations.  Please remember that Anon and Cohn, and others, have advanced this important argument primarily based on the results of long-term appropriately powered drug trials.  The CorCap device is not a beta blocker or an ACE inhibitor.  In addition, the dimensional changes observed in this trial are not associated with a reduction in mortality or hospitalizations.  
		Dr. Pina has indicated that the dimensional changes induced by the CorCap device are not strongly correlated with any clinically meaningful changes in a host of standard heart failure variables that were measured in this trial.  
		The sponsor also states that the safety has been established with the CorCap, but acknowledges that the learning curve for acute placement of this device is an issue.  Perioperative mortality after device placement in the no-MVR group appears to be decreasing over a several year time span, lending credence to the theory that the safety profile associated with this device may have improved, or has it?  
		Please do not forget how the limited sample size and time-related changes, and the characteristics of patients being enrolled in this trial may confound our ability to interpret whether the up front mortality and morbidity costs have really been impacted in a meaningful way.  Have we considered the impacts of optimal patient selection on perioperative mortality?  The sponsor has initiated this process with the focused cohort analysis, but as Dr. Thompson has pointed out, many questions remain regarding the validity of their conclusions.  
		Let us also not forget the long-term cost associated with use of this device, including the inability to perform future CABG operations, the added complexity for re-operations in patients with the CorCap implanted, and the risk of chronic pericardial constriction.  These concerns cannot yet be addressed with the current data.
		Based on our review of the totality of the data, FDA does not believe the risk benefit profile of the CorCap supports and approval decision.  The sponsor has attempted to address this issue by conducting a post hoc re-analysis to identify a population in which the risk benefit profile of the CorCap is maximized.  The sponsor has stated that this post hoc analysis is not necessary for approval.  However, the indication statement proposed by the sponsor is based on the focused cohort analysis.  While FDA believes this analysis provides a hypothesis for future study, it cannot be used to define the dimensional parameters that objectively indicate an optimal patient population for use of the CorCap.
		The sponsor has also proposed to conduct a 500-patient post-market study as part of the basis for approvability of the PMA.  Please remember that pre-market requirements for safety and effectiveness cannot be transferred to the post market arena.  A reasonable assurance of safety and effectiveness must be established prior to market approval, so where do we go from here?
		FDA believes the sponsor has acquired useful data from the initial Acorn trial, but FDA has concluded, along with the Advisory Panel, that the safety and effectiveness signals are not yet clear enough to justify an approval at the present time.  They remain committed, though, to designing and implementing a subsequent trial that will allow a more definitive assessment of the safety and effectiveness of this technology.
		We look forward to the ensuing discussion regarding your interpretation of the data and the issues in dispute.  Thank you.
		DR. RAMSEY:  Thank you.  Any other comments from FDA?  You have a bit more time, if you're interested.  If not, then again, as with Acorn, we're open for questions from the panel, clarifying questions from the panel to the FDA.
		DR. LASKEY:  We've heard repeatedly from the sponsor's statistician advising us not to concentrate on P values, which hopefully we don't, and to look at the raw data, so I would like Dr. Thompson to speak to me in clinical lingo, that how does one equate or equalize odds ratios of 1.5 and 2.5 into the same treatment effect?
		DR. THOMPSON:  I imagine you're referring to the differences in the odds ratio between the two strata.
		DR. LASKEY:  Correct.
		DR. THOMPSON:  Well, for a clinical interpretation of those two odds ratios - well, for example, the 2.5 odds ratio would be that the CorCap group has a 250 percent chance above the control group responding in a better category, and then we reduce that by 100 percent in the MVR group.  Perhaps, I have them reversed, so we're talking about a much bigger chance in one stratum versus another.
		DR. LASKEY:  Well, I'm sorry.  I didn't mean to put you on the spot, and I certainly don't mean you to dumb down here, but it's the location and the width that I pay attention to.  And the width of the confidence intervals for the non-MVR strata are wide.  They're wider than they are for the other strata, so I tend to have less certainty when I see that.  
		Secondly, when I see an odds ratio that's that that much greater than its other strata, I say gee, that's a tremendous improvement over the MVR strata treatment effect, and so we're told that well, there is no appropriate statistical test, I guess, CMH, or Breslow data, or whatever you're going to do to say that they're homogeneity or not.  But if we can't do that, then are we going to walk away from this saying that the bang for the buck is in the non-MVR strata?  That's what I'm after.
		DR. THOMPSON:  Well, it is true that -- the sample size is probably not large enough to show that there would be a significant difference between those two strata.  I think one of the main points of our presentation was to just highlight the clinical implication with regard to just the observed treatment effect.  Certainly, you're going to see more uncertainty when you have a lower sample size, as you would in the no-MVR group.  Statistically, I can't say that one is, in fact, better than the other, that it's statistically significant, and that was one of the primary reasons why I didn't discuss that result, but Ileana Pina discussed the result.  So I'm sorry I couldn't be more definitive statistically with regard to which one is better than the other, but that's just the way it is.
		DR. LASKEY:  So, as usual, it falls back to the clinician.
		DR. THOMPSON:  Well, it's not -- I don't know if I want to say as usual it falls back to the clinician.  It's just that I can't give a statistical yes or no.
		DR. LASKEY:  That's fine, thank you.  There are some things that defy statistical interpretation, and this is one of them.  When you have a population which two-thirds received mitral valve intervention, and you're making conclusions which are driven by the group that didn't get the mitral valve intervention.  I'm just struggling with that.
		DR. RAMSEY:  Any other questions?  Yes?
		DR. SACKNER-BERNSTEIN:  I would just like to get a response to a perspective from the FDA.  I understand why each of the risk elements has been defined, but I'm a little bit curious about the focus in the documents, as well as the inclusion in the discussion about pericardial constriction.  And the reason I raise that concern is that, it seems hard for me to believe that a study anywhere near this size, or perhaps even ten times this size, would have a likelihood of detecting it, even if it were there.  There's very little literature on post op risk of constriction.  One series I could find was just straight bypass procedure, where 5,000 patients, I think it was about 11 that had it on follow-up.  I mean, I understand why there's a concern about mortality risks even in a population of 300.  What do you think the reasonable expectation would be to rule out effect on, or finding constriction with a device like this?
		DR. ZUCKERMAN:  Pre-approval low, and I think at the time of the first Advisory Panel meeting, certainly that was understood, if everything else felt in place.  We're just indicating that as another safety concern.  AS you know, Dr. Yancy in his remarks, pointed out quite appropriately that we were in this room last week with the drug alluding stent situation, where at three and four years we're seeing a remarkable and unfortunately big, and unexpected safety problem with a chronic implant.  What has impressed us is that while there was a great amount of animal data that was performed in this application, the human results do not seem to reflect it in the amount of dense fibrosis that's apparent post surgery, and what is the potential long-term impact of that?
		While Dr. Piantadosi tried to suggest that there's a very low rate because he assumed a linearized right model, what we saw with the drug alluding stent situation last week was the occurrence  of an unexpected, very significant increased hazard ratio at a period of two to four years, so it's just another unknown that fits into the safety category.
		DR. RAMSEY:  Okay.  We're running a slight bit behind, and we do have another open public hearing session that can last up to 30 minutes.  If we don't take 30 minutes, I may take the Chair's prerogative to ask a couple of questions, but I want to move us along.  So, at this point, we have opportunities for others to come and testify.  For the open public hearing, speakers who wish to do so, should keep their comments to 10 minutes.  And if anyone does wish to speak, please adhere to the rules for the first open hearing, which is to state your name, your institution, financial affiliation with the sponsor before you make your comments.  Thank you.
		DR. BREWER:  Thank you.  I'm Robert Brewer, I'm a physician, and the Director of the Circulatory Assist Device Program at Henry Ford Hospital, and I'm being reimbursed for time and travel, but have no equity interest in Acorn Cardiovascular.  I have a clinical practice oriented heavily towards surgical interventions for heart failure, and have been actively involved in a variety of device investigations in our clinical laboratory with Tony Sheebach.  And I just want to make a few brief comments on where I see this fitting in our clinical practice.
		There's a significant surgical focus on interventions for end-stage or Stage D heart failure.  The striking fact about these therapeutic options, the longer we're in practice, is that they have a significant limitation on long-term survival.  Cardiac transplantation is our gold standard, has about a 50 percent median survival, and only 15 percent of the patients, only 20 percent of patients are still surviving at 15 years.  Transplantation remains extremely limited in scope and availability of donor organs, and we have great optimism for the future development of mechanical circulatory assist therapies, but they come nowhere close to the outcomes for cardiac transplantation to date.
		These observations highlight the great need for therapeutic options for patients who have progressive heart failure, despite the optimal medical management that Dr. Yancy referred to.  In addition, to improve functional status I think is very important that our goal is to delay or halt the progression of the sort of advanced Stage C patients to that end stage of heart failure.
		I've been involved with pre-clinical studies of the Acorn CorCap, as well as the clinical trial, and I've placed about 10 of these devices in patients.  The role I believe of FDA panels and studies is to evaluate devices that show promise, and determine if we find them safe and effective, as we've heard today.  In the pivotal trial of the Acorn CorCap, I certainly believe a straightforward analysis of the data shows safety and efficacy.  I understand that alternative analyses of the data may show benefit that's greater or lesser than we would ultimately desire for certain patients, but I think that's true for almost all studies, and certainly almost all devices.
		A key observation to me, as a heart failure surgeon, is that significantly fewer of these CorCap patients required cardiac transplantation or implantation of a ventricular assist device.  It's also important to note that the CorCap didn't preclude these later options, as a number of patients underwent successful transplantation or VAD implantation, and similarly, Dr. Bolling and Dr. Acker have transplanted a couple of these patients with findings of moderate to significant adhesions, but not different than we see in our routine re-do VAD patients getting cardiac transplantation.
		The Acorn CorCap offers a new approach to heart failure therapy, and I strongly believe as a clinician that this device has surpassed the threshold of reasonable assurance of safety and efficacy.  That is the standard for approval, not our best case expectations, or the known outcomes of existing technologies.  I believe that CorCap should be available in our tool box for interventions for appropriate Stage C heart failure patients.  We have limited options, very limited options for these patients who have optimal medical therapy, and continue to have progression of their heart failure syndrome.  I think this novel therapy has been shown to improve functional status, and to slow the progression of the heart failure syndrome; thereby, decreasing the necessity for our even more limited end-stage interventions.  I thank you for the opportunity to speak.
		DR. RAMSEY:  Thanks.  Is there anyone else who would like to come to the -- again, please state your name and affiliation, and financial relationship with the sponsor.  Thank you.
		DR. GROSSI:  Certainly.  I have a slide, please.  My name is Dr. Eugene Grossi, Professor of Surgery at New York University School of Medicine.  I have no disclosures.  My research group and myself have no potential conflict of interest with this device or sponsor.  I'm here on my -- paying for myself, and I was asked by the FDA to come here and give public comment based on a recent editorial I wrote in one of our journals regarding the mitral valve strata of the Acorn.  Next slide, please.  
		From the perspective of a clinical and investigatory cardiac surgeon, the mitral valve stratum of CorCap collected very important data for us in a very systematic fashion.  We just have to quickly review the patient cohort.  We're talking about patients 53 years of age, solid New York Heart Class III no matter how you cut it.  Ejection fraction is 23 percent, end-diastolic dimension of 70 millimeters, impaired six-minute walks of 340 meters, and elevated end-diastolic volumes of 270 Ccs.  These people have peak VO2s of 14 Ccs kilogram per minute.  		The results were spectacular, 30-day mortality of 1.6 percent, and one year survival of 86-1/2, and two-year freedom from all-cause death of 85 percent, with significant improvements in exercise columns, and changes in end-diastolic volume.  In summary, they're able to show in this overall study low procedural mortality rate, significant improvements in quality of life, exercise performance in New York Heart Class.  Equally as important, there was evidence of reverse remodeling.  The mitral valve operations led to improvements in LV functions and shape.  And, finally, it showed us that these operations were durable.  Recurrence of clinically significant MR was uncommon in this cohort, unlike previous reports.
		What's the significance of this data?  There is no randomized control data showing us the benefit of mitral valve repair in this cohort of cardiomyopathy.  This paper and the data it contains is one of the increasing number of reports supporting clinical benefit to this therapy.  
		Until recently, clinicians have had very little data.  We look at American Heart guidelines from 1998, determining the surgical candidacy of the symptomatic patient with MR, and advanced LV dysfunction.  It was a common clinical dilemma.  If a repair appears likely, surgery should be contemplated, provided the ejection fraction is greater than 30 percent.  In the recent guidelines this is still "under development".  
		Even earlier this year, the American College of Cardiology sponsored a controversial continuing medical education course entitled "Mitral Valve Surgery for CHF - A Failed Concept".  This course espoused the opinion that surgical treatment of functional MR results in little, if any, reverse remodeling.  There is uncertainty based on the University of Michigan data.  Steve Bolling has taught us a lot about mitral valve repair; however, there was a propensity analysis that came out last year in JACC that looked at transplant-free survival doing a retrospective analysis from their record database.  They found no change in intermediate term survival.  This study was problematic.  It was confounded by indication, unobserved covariates, no information about the adequacy of medical therapy, improvement in symptoms, durability of repair.  There were different time endpoints of the study, depending upon whether the patient was a medical or surgical patient.  However, this is a manuscript that has been touted as hard evidence that treating MR in these patients has no benefit.
		So the question that's really here before us today is, what did Acorn add for these patients?  I'm not here to argue statistics.  I learned a lot listening to Professor Rubin this morning, but to give clinical perspective.  I don't think there's any argument here that we're seeing a difference in survival.  We are seeing a differential improvement in clinical endpoints.  These patients did better.  Additionally, we're showing that there was a differential improvement using the CorCap device in these patients in terms of end-diastolic volume changes, and shape changes.
		What does this mean?  Well, we'll go back to  J. Cohn who was quoted earlier, "Clinical and experimental data document that structural changes correlate with progressive worsening of the syndrome of heart failure, that these changes are preventable and reversible, and that a favorable clinical therapeutic response is associated with the regression remodeling."
		Are there concerns?  Yes, there's the potential long-term adverse effect, the risk, and the difficulty of later transplant, and this has to be balanced by the surgeon.  However, it's not my primary concern, and not of any of the primary concerns of any of the surgeons we heard here today.  We have to look at the magnitude of these patients.  We have over half a million patients of heart failure a year, yet only 2,000 of those patients are going to get a heart transplant, and this number has been unchanged for a decade.
		My concerns with Acorn, the unknown performance in ischemic cardiomyopathy patients, unknown long-term graft patentcy; however, these aren't coronary patients.  I will disagree with something I heard earlier this morning.  Somebody said these aren't patients like patients with cancer.  That's absolutely wrong.  If you at patients with severe MR, this cohort of patients, half of them are dead at five years, even with the best of therapy.  This is exactly like patients with cancer.
		I think study suggests there's clear benefit to the surgical elimination of mitral regurgitation, that there is an additional clinical benefit with CorCap support device, given the improvement in left ventricular structure and function, along with a very low mortality rate, physicians should strongly consider offering mitral valve surgery in combination with the device to support patients with non-ischemic heart failure and mitral insufficiency.  Thank you for the opportunity to talk.
		DR. RAMSEY:  Thank you.  Is there anyone else that wishes to give a discussion or testimony?  If there are no others, then we can begin the panel discussion portion of the meeting.  This portion is open to public observers, but public attendees may not participate, except at the specific request of the panel.  
		At this point, the panel may ask questions of the sponsor or the FDA, or the public during this portion of the meeting.  However, the ground rules are that there can't be direct debate between the sponsor and the FDA.  And before we begin this part of the discussion, I want to repeat the panel's charge.
		The panel is charged with answering the following question, and to make a recommendation to the Center Director as to how this scientific dispute should be resolved.  Dr. Braier will have a slide of this on the screen for the panel members to refer to.  So the question is, does the PMA, as amended, provide valid scientific evidence that demonstrates a reasonable assurance of the safety and effectiveness of the CorCap CSD for its intended use in the original patient population, and/or the focused cohort?
		In considering that recommendation, the panel is asked to determine the following; whether the overall trial results for the primary effectiveness endpoint are interpretable and clinically meaningful, whether the secondary endpoint results are supportive of the safety and effectiveness of the device; third, whether the FDA's safety concerns have been addressed by the data provided.  And, finally, whether the data submitted by Acorn adequately addresses FDA's safety and effectiveness concerns for the original patient population, and/or the focused cohort.  So let us look at each of these questions, and its component questions regarding safety and effectiveness as a way of framing the panel's discussion.
		Okay.  So, perhaps, what we can first do is focus on the overall trial results, number one, for the primary effectiveness endpoint, and discuss whether we feel they are interpretable and clinically meaningful.
		DR. SACKNER-BERNSTEIN:  As we're starting, I'd like to ask a question to Dr. DeMets about the approach to imputation with the NYHA.  It seems to me that a key component of that analysis is an assumption referred to as the missing at random assumption which, from my understanding, would imply that there is no basis to presume, or maybe I'd use the term reasonable.  There's a reasonable assurance that there's no basis to presume that there's a difference in the patient population over the course of the study.  I'm curious as to whether we can make that assumption for a couple of reasons, and the two reasons include this; first, there are other clinical trials where despite looking for a reason as to why risk may change, or the population, or the difference in treatment effect may change over time, we can't find any.  As an example of that, there's the AheFT study, which looked at Hydralazine and Isordil in African-American population of heart failure, where over the course of the study, the differential effect between treatment and control was different over time, couldn't be explained despite the entry criteria over the course of the study being the same throughout, and all the baseline clinical characteristics between that early and late group being the same.
		An example of where those standard kind of characteristics were not able to detect a difference in patient outcome and treatment effect, so in that trial, certainly, you could not use a multiple imputation methodology with a missing at random assumption in place.  
		The second thing is that there's one characteristic of this trial that in my mind, and this is what I want to ask Dr. DeMets about, particularly, which in my mind challenges the missing and random assumption in this trial - in April of 2002, there was an investigators meeting held, where it became evident that there might be a problem with the preoperative mortality in the no-MVR group, where there were four post op periop deaths in patients off cardiopulmonary bypass, and a recommendation was made that - I don't know exactly what the wording was, but it had something to do with recommending that surgeons consider performing the operation differently.
		As soon as a recommendation goes out to investigators to do something differently at such a crucial part of the trial, it seems hard for me to imagine that one could be assured that there wasn't some difference in the way patients may have been selected or treated.  So, in that case, would that past experience with AheFT, and/or that concern about a potential change in operative procedure mean that the missing at random assumption may not be valid?
		DR. DeMETS:  I'm glad you started off with such an easy question.  Well, let me just say a few comments about the imputation process, and to start off with - no, I'm not sure I can assure you that these changes don't have some impact, but in general in clinical trials, we work with a hard to get - pick endpoints, for example, that we can get complete ascertainment so we don't have to have this challenge, but as you pointed out, it happens anyway.  
		Despite, I think, the popularity and the validity of this methodology in many settings, I think we try hard not to have to use that methodology in the clinical trials for the reasons you've talked about.  And I don't think it's common practice, actually - at least not with cardiology areas that I'm familiar with.  The missing at random assumption is a strong assumption, and as was addressed earlier, because this was sort of systemic, it was the first 174 patients - on that basis, one would believe that the assumption is probably quite good and valid.  		The issue you raise, however, is - and it's common that patient characteristics do change over time, even without the kind of interruptions as you've mentioned, especially if there's something that's different, like change in policy, or change in methodology over time.  I can't assure you that that doesn't have some impact.  It's not my most major issue, but I can't assure you that it couldn't have some effect.  I am assured, though, that the different multiple imputation techniques all - without worrying about the specific P values - give you some robustness.  I mean, it doesn't really matter from a qualitative sense, what you do, you get the same general answer.  The estimates do not differ all that much.
		DR. RAMSEY:  Any questions from the Consumer Industry Reps?
		DR. HUGHES:  No questions.
		DR. RAMSEY:  Please, if you have more, I have some of my own, but I'd like to hear from the other voting members.
		DR. LASKEY:  Well, maybe an easy one for you, Dr. DeMets.  But can you just go through as how the ordinalization, if there's such a word, of an endpoint affects its statistical robustness?  What are we losing by using an improved, same, or worsened, which is derived from changes in variables, some of which are continuous, and some of which aren't?  What does smushing all these things together into one of three categories do for the rigor?
		DR. DeMETS:  Again, it's nice you ask easy questions.  This particular end - well, let me start out, I have trouble with the primary endpoint.  We've used similar kind of endpoints in other studies.  I've been doing heart failure trials since the late 1980s, I guess, but there never is a primary, there is certainly secondary endpoint to see how an endpoint of this type would follow the primary endpoint.  The reason there were never primaries, because you are mixing things together, mortality, hospitalization, or procedures, as well as change in heart failure status.  So these are hard to interpret in any kind of simple way.
		The issue of ordinalizing it, I mean, there was a discussion earlier about using rank test versus other continuous tests.  You don't really lose all that much by the rank test, they're pretty robust.  But if you want to say how do you interpret a mixture of continuous and ordinal data, improved, not improved, that's just a hard one, and I said that's why I don't think we use that endpoint, typically.  More likely we'd use something like death and hospitalization, or death, hospitalization and other things, and have left that to sort of a secondary role.
		DR. RAMSEY:  I would like to ask a question of Acorn.  The FDA in much of their discussion emphasized that in their opinion, the degree of clinical benefit was much less than was expected for many of the endpoints, including the primary endpoint, the New York Heart Association classification.  And I didn't really hear in your rebuttal any response to that issue about whether you felt that the changes that they showed were accurate, and whether you felt that they were clinically meaningful.
		DR. MANN:  I'm going to address this in part, and then pass it to my colleague, Dr. Jessup.  First of all, the changes that Dr. Pina showed were in secondary endpoints that the FDA did not approve.  Second, I want to emphasize the totality of the primary endpoint and the point that we've tried to emphasize is that you really can't dissect apart or deconstruct the primary endpoint, because it was intended to be analyzed as a whole.  If you look at the odds ratio for the primary endpoint, there's a 76 percent greater likelihood that people will be in a favorable category after receiving the CorCap.  If you want to deconvolute it more than that, it becomes a little bit difficult to do it, because it really wasn't powered to look at specific changes in New York Heart; so, again, I think one argument would be that we look at the totality of the effect, and the magnitude of that effect was, in our opinion, clinically significant.  The changes in the secondary endpoint, such as LVEDD, I mean, we could sit here and argue all day about what's a clinically significant change in LVEDD in a patient on ACE inhibitor and a beta blocker who is 75 years old.  Those numbers, I think, are arbitrary.  Mariell, do you want to comment further?
		DR. JESSUP:  Thank you.  I think it is important to reflect on what is that we hoped to happen for these patients.  These are patients that are already on maximal medical therapy, so let's assume that some of those will stay the same.  That's what we could hope.  And for those that we were hopefully intervening in before something bad happened, what would happen bad?  And, hopefully, our composite endpoint captures that.  
		One, they'd feel worse, and we believe that the New York Heart Association, and the Minnesota Living with Heart Failure, and the SF-36 captured that, that, in fact, with treatment they had less feeling bad, or they could die, or they could really deteriorate and need transplant or a VAD.  I mean, those are the things that happen to these patients.  And in this composite, which is still the way we have of looking at what happens to heart failure, the composite was a positive and statistically significant effect.
		All of heart failure trials have struggled with what is meaningful to the patient.  Mortality in a huge trial is meaningful to us, it's not meaningful to the patients that died, and so I think in the absence of a trial powered for mortality, we are obligated to take some kind of composite endpoint.  In the absence of being able to use structural endpoints as the single endpoint, we are obligated to take a functional, and structural, and mortality endpoint, which is what we did.  And I think that this was a meaningful result.
		DR. MANN:  And I'd also like to pass the microphone to Dr. Starling for a second, since you did ask - were allowed to introduce, I believe.  We now have three-year data follow-up on the durability of the end-diastolic volume changes, so I'd like Dr. Starling to address that.
		DR. STARLING:  Thank you.  I just wanted to address your question with respect to the end-diastolic volume, which probably applies to other structural measures.  And as has already been emphasized, unlike some of the more dramatic acute remodeling procedures that we and others have reported partial left ventriculectomy and surgical ventricular restoration, where you can measure a marked difference when the patient leaves the operating room and the volume and the dimension.  This is clearly a situation where it's more subtle, and it evolves over time.
		All that has been presented to-date is 12-month data, but certainly there's additional data that will be presented at subsequent meetings based on the long-term follow-up that does show progressive changes that occur.  
		DR. MANN:  Dr. Piantadosi wanted to make a further comment.
		DR. PIANTADOSI:  I wanted to make just one quick comment regarding the primary outcome, apropos of Dr. Laskey's earlier question.  The primary is not a mixture of categorical and continuous effects.  All three components of it are categorical, you're either alive or dead, you've either had a procedure or not, and you're some category of NYHA.
		DR. RAMSEY:  I wanted -- I am going to give the FDA a chance to respond, so bear with me for just one more moment.  I have one more question for Acorn, which is, whether they agree with the FDA's assertion that really the driver of the difference in statistical significance for the primary endpoint was change in major cardiac procedures, and your interpretation of that, if you agree.
		DR. PIANTADOSI:  I'm not sure I would say it that way as a conclusion.  If you tease apart the components that go into this categorization, you see the most differences in that particular component.  That's true.  However, I think of this outcome more as an algorithm, rather than a fancy, difficult to interpret outcome.  And in that algorithm, being alive or dead plays an absolutely critical part, so even though there's not a difference in mortality, it's very foundational for you to be in either the same category, or the improved category.  So the fact that you're not driving mortality differences, for example, doesn't mean that it's absolutely - that it's not absolutely and fundamentally critical for the interpretation of the outcome.  So yes, deconstructed, the biggest difference is in the major cardiac procedures, but as an algorithm, they're all equally important.
		DR. RAMSEY:  Okay.  Now, FDA, please, if you would like comment on that, those questions and responses.
		DR. ZUCKERMAN:  Okay.  We've like to, again, remind the panel about what the dispute is about.  The dispute is about the data that was submitted up to the issuance of the second not-approvable letter.  You've just heard about additional data that have not been reviewed by the FDA, and cannot be verified.  Matt would like to make an additional comment.
		DR. HILLEBRENNER:  Yes. I think the original question pertained to the components of the primary endpoint, and specifically looking at the - also, at the NYHA component.  Now the sponsor has commented regarding deconstructing, to use their words, the primary endpoint.  However, obviously, we may disagree on this, but the FDA has some questions regarding the primary endpoint result; therefore, we feel the need to rely on what were pre-specified supportive analyses to look at the additional components individually.  And we talked a lot about mortality, and I think we agree that mortality in this trial was powered to be a safety endpoint more than effectiveness.  However, there was no difference in the number of patients that had died by the common closing date in the study, so even if there was a slight difference in mortality, even though it wouldn't have been significant statistically, we may have accepted that something was happening, so there was no difference in mortality, which questions the LV reverse remodeling hypothesis.  But the other - we have the NCP component, which we would agree that drives the statistical analysis.  The other component is the NYHA, which the sponsor has presented using CorCap for their primary endpoint, and we asked them questions regarding the validity of that.  And if you use site-assessed NYHA, which was a secondary endpoint, more patients improved in the control population, a higher percentage in site NYHA than did in the treatment group, so that is some of where we're coming from in terms of there's a questionable benefit even to NYHA.  And I will go ahead and show a couple of slides for that.
		So using imputation, if you look at only the core lab NYHA component, there's about a 10 percent greater chance of improving in the treatment arm, which equates to 56 over 42 patients.  However, if you look at this analysis only using site NYHA, we have a different result, which shows basically the same.  I mean, technically, it's higher in the control, but I think we'd all agree that that's equivalent.
		Again, getting back to our concerns, I know it's been alluded to earlier, and we still have yet to  discuss it, but our concerns regarding what does core lab NYHA truly mean?  And I'll defer to Dr. Pina for additional comment.
		DR. PINA:  Thank you.  First of all, I want to agree with Dr. Jessup and with Dr. Mann, it is extremely difficult for us in heart failure to always find meaningful clinical endpoints, and to try to determine what the differences should be.  But I think we learned from other trials that we've done in the past.  And, for example, with the Minnesota Living with Heart Failure Questionnaire, which is a questionnaire specifically developed for heart failure patients, which has been much more sensitive in the past than other questionnaires.  We consider in general, clinically meaningful changes less 5 or more decrease in the score, treatment versus control.  If you go into the CRT literature, it's there.  It is also true that in device trials, in any trial where there's an open label treatment, there's usually more missing data and the people who feel like they lost because they did not get the treatment, or the device, or whatever the intervention is, so that's true, that's not unusual.  But those differences for us to be clinically meaningful need to be established, and I think at least for the Minnesota Living with Heart Failure Questionnaire, that's been pretty well accepted.
		DR. RAMSEY:  I do want to remind Acorn that we cannot have new data presented that hasn't been shared with the panel or the FDA, or even intoning that there is new -- 
		DR. MANN:  I apologize.
		DR. SACKNER-BERNSTEIN:  A statement has been made by both parties that there's no mortality difference here.  I'm concerned about that statement, even though I see that the actual numbers of deaths up to the common closing date are the same number.  And I'd like comments - responses to a couple of comments.  First of all, it looks as though the study was designed with the intent of excluding anything more than a 15 percent increased risk of death over the course of follow-up.  And along those lines, it appears to me from looking at the numbers, and doing a very, very poor man's tie square, that you probably have an odds ratio that wouldn't be that wrong with an upper confidence interval of about 1.5, 1.55.  I don't know if that upper confidence interval of the odds ratio is correct or not, so I'd like to start with the sponsor telling me what's the upper confidence interval for the risk of death in the patients randomized to the CorCap, versus control, up to the common closing date, because that would tell me what safety bounds has been established for this device.
		DR. PIANTADOSI:  I'm sorry, I can't do the arithmetic in my head, but based on the event curves that have been shown repeatedly in the discussion, the risk ratio in the two treatment groups is essentially 1.0.  The upper confidence bound on that hazard ratio could be calculated from the number of events, which I'm sorry, I don't know.  But the point estimate is equality.  I'm not sure if your question is saying that we should be interpreting a mortality difference in terms of the extremes of the confidence interval or not, but I certainly would not support that as the primary interpretation of an equivalent mortality in two groups.
		DR. SACKNER-BERNSTEIN:  I think that I'm quoting correctly the study protocol, which specified that the population size that was committed to in this trial would be sufficient to exclude a mortality risk of greater than 15 percent, so as I understand it, the way you do that to show whether you've met that pre-specified limit, is that you calculate not only the point estimate, but you do look at the extremes of the 95 percent confidence intervals.  And I would expect to see the upper boundary of the 95 percent confidence intervals to be equal to 1.14 or less, if that pre-specified safety criteria were met by the data in this trial.  That's my understanding, and that's what I'm trying to get at.
		DR. PIANTADOSI:  Okay.  So you may be correct in your reading of the protocol.  Again, this minute, I don't have it in front of me, but there is a fundamental point here about how you interpret the data in light of design assumptions that may have been made before any data were in-hand.  Although the trial might have been designed to give you a reliable detection of a specific treatment effect, those assumptions are now irrelevant when the data are in-hand.  And the way to reason through a potential mortality difference is to look at the point estimate of the relative risk for mortality, which, as I said, is approximately one, and the confidence interval around it, which I don't know.  It may or may not be consistent with 15 percent. But I think all the information you need to make an assessment of mortality is contained in that point estimate and confidence interval.  And assumptions made before data were collected are now irrelevant.
		DR. SACKNER-BERNSTEIN:  Could the FDA comment, because while I agree with the last statement, I don't see the confidence interval supplied anywhere in the document.
		DR. ZUCKERMAN:  Yes, Dr. Sackner-Bernstein, thank you for asking that critical question.  I'm going to ask the panel members to refer to, I believe Slide 93 of Dr. Thompson's present - of the FDA presentation, and we'll quickly review the perspective that we utilized in CHF device trials for this critical mortality question.  And it gets back to understanding the totality of the data.  We never want to forget mortality, whether it's part of the primary endpoint or not.  
		I believe the 15 percent value that we initially - that the sponsor initially wanted to protect against resulted in a sample size calculation of 180 patients.  You'll note from the attachments and records that we've provided you in Volume II of our panel pack, that we felt that even with such a protection given the primary endpoint, that that was too wide, and we settled with the sponsor for a 300-patient sample size that would protect against a difference of greater than 10 percent.  The Greenwald estimates for the Kaplan-Meier analysis are on this slide, and you'll see that that's about where we ended up, roughly.  And the key thing to consider is given this final result, and the symptomatic improvement, what do you make of it at the end of the day?  
		The other thing that I would point out is that at 30 days, the perioperative treatment minus control difference does not include zero.  Dr. Thompson, any other further -- 
		DR. THOMPSON:  Yes.  I'd just like to make one correction to what Dr. Zuckerman said.  These are the confidence intervals on the difference in proportion between treatment and control at each of those cumulative time points.
		DR. PIANTADOSI:  So could I interject something here?  I think this is exactly what I said.  The treatment to control hazard ratio is one, and the confidence interval is - we can't get it exactly on the hazard ratio here without some mental arithmetic, but it's perfectly consistent with a null. I'm not sure what other information is implicit in the question that's not contained in that fact.
		DR. RAMSEY:  Steve, I'm sorry, but you only are able to speak if we ask a question of -- 
		DR. PIANTADOSI:  I'm sorry.
		DR. ZUCKERMAN:  The FDA would just point out that the confidence interval presently, with the presently available data, is wide.
		DR. RAMSEY:  Again, I want to turn to industry.  And this conversation is, in my mind, quite esoteric.  I wonder how many folks out there are wondering what we're doing, but I want to encourage you to not feel inhibited for asking questions that you might be worried are somehow dumb, because I doubt they are.  So please, don't hesitate to ask.  But, otherwise, we'll go on with more questions.  I have some too, but please, Jonathan, go ahead.
		DR. LASKEY:  I'm not -- on this last theme, I'm not sure where the agency is; although, I think I can read Dr. Zuckerman's mind, but he hasn't said this.  But, first of all, just as an amateur wading into this treacherous terrain, you can't really divvy up a Kaplan-Meier curve like that.  The overall statistic is the overall statistic.  It's the whole composite, it's the cumulative event rate that you compare over the whole curve, but can you just sort of slice it like this and look at individual time points, and say as I'm looking at the curves, well, they cross.  And if they cross, what that means?  Can you do this exercise legitimately?
		DR. THOMPSON:  Well, first of all, we're not divvying up the Kaplan-Meier survival curve estimate, we're looking at proportions of death up to particular amounts of follow-up time.  And I think the point to be made about this slide is that you don't see really that much difference.  The confidence intervals clearly cover zero at the common closing date. I think that's the main point of the slide.  And, also, the way in which this component is shown is the way in which it was represented in the composite endpoint.  Each death counted as one, and so the 25 deaths for each group were 25 in the worsened category, and that's the primary reason why we showed the slide the way it's shown.
		DR. LASKEY:  Okay.  So to an idiot, this is not a time to event analysis.
		DR. THOMPSON:  No, it's not.
		DR. LASKEY:  Okay.  Thank you.
		DR. RAMSEY:  Okay.  Any other comment?  Let me ask another question.  I hate to be a splitter versus a lumper, but -- oh, if we could turn off that slide for a moment, please.  I still - and this reflects me coming to this trial at this very end stage.  I still have personally difficulty with this composite endpoint, because to me, it's a composite of safety and efficacy data, so it's hard for me not to split things out and try to look at safety separately, and efficacy separately.  And, again, I want to get back to this issue which the FDA raised about time to major cardiac procedures, and their concern that the treatment group had delays for the very reason that surgeons were reluctant to go in and re-operate after the CorCap device was implanted.  And they note that in support of that in their documents, that when one looks at cardiac re-synchronization therapy, that there was actually no difference in CRT placement, which does not require a repeat thoracotomy, as evidence that there might have been some bias against re-operation in the intervention group.  And as I read that, I was thinking about what other outcomes might not be affected that would be an indication of worsening heart failure, and one of them was hospitalization.  And I wondered if you could - whoever had that slide on re-hospitalization rates could show that again for us.
		DR. DeMETS:  I think it's Slide 27 in the Acorn presentation.
		DR. RAMSEY:  Okay.  My understanding - well, that's time to event. I think I have a question about total number of re-hospitalizations, which I'm more interested in, actually.  And as I recall, there was no significant difference.  Now this is all-cause, and we obviously can't tease out whether this is due to heart failure exacerbations, or other problems.  But, to me, it seemed to lend support to the idea that these patients, at least in terms of severity, weren't significantly different in terms of having severe heart failure episodes that required ER visits and hospitalizations.  And I wanted Acorn to respond to that suggestion, and give me your opinion.
		DR. MANN:  Dr. Ramsey, I'm not sure I totally understand your question, that you want me to respond to.  You just said that you didn't see a difference in the hospitalizations, implying that the severity of the groups was similar.  Is that correct?
		DR. RAMSEY:  Right.
		DR. MANN:  Okay.  And the argument that we tried to make, if I'm understanding you correctly, is that if, indeed, patients were withheld or for whatever reason the investigators were reluctant to refer them for transplant, for ventricular assist devices, other procedures, we would expect that more of them would have progressed to Class IV heart failure, and/or have been hospitalized.  We didn't see evidence of that.
		DR. RAMSEY:  Yes.  So the idea would be that if the patients were doing the same, but there was some reluctance to do surgery, you would see less surgery in the CorCap arm, but all the other parameters of severity would be the same, so that would suggest that surgeons are holding back, while at the same time the patients are the same clinically in terms of their progression.  So that was my question.
		DR. STARLING:  Well, just to repeat - our position is that you cannot hide from the endpoint of worsening heart failure, which would have been evidenced by if, indeed, the patients weren't referred  for transplant or ventricular assist device, we would have seen the patients show up as more Class IV heart failure, or, indeed, in the hospital undergoing treatment.
		DR. BOLLING:  If I can help on the answer to that - I'm a clinical cardiac surgeon.  I was not a member of the Steering Committee.  I did not appear at the first panel, and I did not make up this endpoint.  But I think my entire practice is devoted to heart failure, and I think this is a very good endpoint for these patients.  The patients when they worsen in heart failure, are forced to go into one of three groups, they either get worse, or they get a procedure in response to that, or they become dead, and there's no other choices for them.  And when we see a patient, we can't avoid or hide a patient. 
		Now the decision to do a major cardiac procedure on any patient, whether it's after an Acorn or not, is not determined by a single surgeon, so I don't think - especially, I can speak to our institution, that there was very little that I had input about determining whether that patient had some other type of procedure at some other later time.  I thought that the endpoint of this group, this composite endpoint was a great endpoint for the patients that I see.
		I think the avoidance of a major cardiac procedure should not be denigrated as a good outcome for the patients.  If we are able to tell the patients from this composite endpoint that your mortality is about the same, that you will feel somewhat better by our secondary endpoints, and that we can avoid a transplant or a major cardiac procedure for you, I think that gives us another tool in our tool box, as Dr. Grossi had mentioned, to help these patients.
		DR. STARLING:  Dr. Ramsey, if I - with your permission, we can put the slide back up that might clarify the question.  This was the slide that I showed in my original presentation, demonstrating a greater percentage of patients that were improved Class I through III, a 17 percent Class IV, versus 19 percent in the control group, the reduction in the major cardiac procedures, and no difference in death, just to speak to the point that Dr. Bolling just made.  And I would also reinforce that where I practice at the Cleveland Clinic, a patient that deteriorates in a clinical trial, or not in a clinical trial, goes to a committee where a decision is made about deploying these type of advanced therapies, transplantation, ventricular assist devices, specifically.  So if the patient had deteriorated to the point where they needed one of those procedures entailing a high mortality rate, one would have expected them to have wound up in one of these other categories.
		DR. MANN:  Dr. Ramsey, if I may - I think just to reiterate the point with the essence of the composite was that you couldn't run and you couldn't hide, so if somebody withheld a major cardiac procedure, they would have shown up as a Class IV, and that's not what happened here.
		DR. RAMSEY:  Yes, please, if FDA has a comment to that comment.
		DR. HILLEBRENNER:  Yes, if we can put up a slide real quick.  I wanted to speak, and I'll refer in a minute to Dr. Pina - I think we understand the nature of the composite in terms of you can't run and hide.  I think the question really then becomes what does core lab NYHA mean.  If you weren't getting referred for a major cardiac procedure, and you didn't die, but you were still worsening on heart failure, you should have worsened at NYHA, and that's how it should have been captured.  But I think now we'd like to discuss and get to the point we've kind of been jumping around all day, is what is core lab NYHA.
		DR. PINA:  So I think we saw this earlier of the site-assessed core lab, the site-assessed, rather, New York Heart Classes, Class III, where 51 of those who had been Class III were assessed to be Class IV by the core.  And here we see the baseline characteristics of the 91 patients who came in as site-Class III, and we see their Minnesota Living with Heart Failure Questionnaire compared to the 51 that the core lab classed as Class IV, and see the peak VO2 is a little bit higher, the six-minute walk is a bit better.  BNPs are very similar.  Now let's go to the next slide, because I think it is very well worth going back to this BNP issue.  I'm not one that routinely uses BNP on every single patient to follow their clinical course, but I do think BNP points a lot to the level of sickness of a population, and it does give some predictive value, and I think this is the way BNP is emerging in the literature.
		The first four lines will show you the BNP of the four groups.  Following that, is a published Val-HeFT, this was a drug trial of primarily Class II and III heart failure patients.  We see the median BNP.  The article that the sponsor has quoted from Dr. Tang at the Cleveland Clinic, reading into the article the Class III in that population had BNPs of 409, the ESCAPE population, which is another well-published population of sick patients who get admitted to the hospital with decompensated heart failure, the BNP is 1,000.  The AheFT trial that Dr. Sackner-Bernstein has mentioned before, this is the BNP, this was presented at the Heart Failure Society this year, and the Miracle trial, which is primarily a CRT trial that was randomized and had a control group, the baseline BNP was 943.  See the next slide.
		If we look now at the patients who had a major cardiac procedure, but were not Class IV on the last available core lab New York Heart Class, you can see that they're very, very similar between CorCap and control.  This is followed now by patients who improved on core lab, but worsened on site-assessed; again, very, very similar percentages.
		The third line are patients who died, but were a Class III or better on core lab at the last measurement baseline, a bit higher in the CorCap, and the patients, finally, who had a cardiac procedure but had an improvement on core lab New York Heart Class, here we see a difference of 5.2, but we're talking about one out of 19 patients, versus five out of 33.  So I think putting the patient population into context is very, very helpful.
		DR. SACKNER-BERNSTEIN:  On that slide right there, the last slide, so these are people who've had a core lab assessment, either imputed or not at baseline, and another one at 12 months, and then had a major cardiac procedure after 12 months?
		DR. THOMPSON:  I calculated those numbers.  This last row is - now this is according to the data set that was given to me by the sponsor.  For the patients who had additional major cardiac procedures, 19 in the CorCap group, and 33 in the control group, one of them in the CorCap group apparently improved from baseline on their core lab NYHA to 12 months in the sponsor's data set.  Now I haven't verified this with the sponsor.  There may have been some sort of mistake in that calculation, but according to the labels on what they call the variables, and what I calculated, these are the numbers I calculated.  And what I wanted to point out in this slide, is that we don't really know what core lab NYHA is measuring.  In all four of those categories, you have inconsistencies with regard to who would be normally considered as having heart failure patients perhaps with major cardiac procedures, or who died, but there's inconsistent measurements on NYHA.  And it's not really to point out differences in CorCap or control, but just to show that it happens in both groups, and it leads to a question of does core lab NYHA class measure heart failure?
		DR. SACKNER-BERNSTEIN:  The only concern I would have is if some of these patients had their cardiac procedures before month 12, maybe that's the reason they're improved.
		DR. THOMPSON:  I don't believe that is the case. I believe that those particular patients in the last row, those were the values on core lab NYHA prior to the major cardiac procedure.  I can't be sure, though.
		DR. HILLEBRENNER:  And I think this just goes back to we have inconsistent results between core lab NYHA and site NYHA, as well.  I think Dr. Maisel would like to make a comment, if that's okay.
		DR. RAMSEY:  Why don't we let Acorn - I think I saw some body language suggesting they wanted to respond to that, and then Dr. Maisel.
		DR. BECKER:  Thank you.  Well, we can have Dr. Kubo describe the core lab NYHA for you.  He has some data.  And, also, while we're pulling up those slides, Dr. Piantadosi wants to clarify something.
		DR. PIANTADOSI:  I would just like to point out that these analyses that the FDA has just shown are stratified on outcome variables.  They are, essentially, completely meaningless.  
		DR. RAMSEY:  Please state your name and affiliation, again.
		DR. KUBO:  Yes.  I'm Dr. Spencer Kubo, and I'm employed by Acorn Cardiovascular, and I'm very pleased to provide some additional information regarding the details of the NYHA core lab instrument.  I appreciate your patients, Dr. DeMets, for waiting for this information.  
		I think we can all agree that the NYHA is the most commonly used method to assess disease severity and patient functional status.  The problem with the NYHA classification is there is no standards for doing this, and it's done differently by different clinicians.  There are many clinicians in the audience.  I venture to say that all of you probably use different questions, and perhaps even on the same - the same person might use different questions among different patients, so we went to great lengths to develop a new instrument that could be used in this trial.  We wanted an instrument that could be used to assess patient functional status in a blinded, consistent, and validated manner.  The methods that we used have been published in a peer review journal, and the details of this are included in your packet, so you can refer to the entire manuscript, but just some very brief highlights.
		First, we used some very common questions that seem to be used by most clinicians asking about patient - about New York Heart status.  As an example, can you - how often do you walk up and down stairs?  If you walk up and down stairs, how often do you get short of breath or tired?  How often do you go for walks on a level ground outside?  If you do go for walks on level ground outside, how often do you get short of breath, or tired?  So the key is that they're very simple questions, but the most important part is that they're the same questions asked every single time this instrument is being used.
		We took this questionnaire to 116 patients in three different heart failure clinics, and had those surveys read by three independent reviewers, and we found very good inter and intra observer concordance.  So when the three reviewers compared their results, they had a 70 to 80 percent concordance.  When the same operator looked at the same questionnaire at a different point in time, of course, masked to what the first determination was, there was even greater concordance, about 90 percent.  So the questionnaire was actually very good; and, in fact, is probably better than what you'd see with standard New York Heart Association.
		Now much has been said in the last few hours about the poor correlation between the core lab NYHA and the site NYHA.  We weren't surprised by that finding, at all.  And the reason is that the site NYHA, as I just mentioned, has no standardization at all.  You can all reflect on how you are taught how to do NYHA, and many of you teach students how to do that, and I venture to say that you're not asking them to do the same way, the same time each and every time you see a patient, so what we needed to do - in fact, the reason why you see no correlation is you're comparing a standardized instrument, using a very consistent methodology, with one which has no clear standards, just a general sense of what to ask, so that poor correlation was expected.
		What was perhaps more important to us as we were developing this instrument was construct validity.  Was it measuring something of value to clinicians who are assessing patients with heart failure?  And I submit to you that it does.  We worked very closely with Tom Rector, who is the inventor of the Minnesota Living with Heart Failure Questionnaire, and I actually worked with him for 11 years when I was at the University of Minnesota, as well.  We took the questionnaire and correlated with other instruments that clearly are important indicators of patient functional status; that is, the Minnesota Living with Heart Failure Questionnaire, the six-minute walk time, and the peak VO2, and we found good correlations, such that as the NYHA status on the core lab instrument worsened, so did the quality of life as measured by a worse Minnesota Living with Heart Failure Questionnaire, a worse six-minute walk time, and a worse peak VO2.  So it does have construct validity, it is measuring something about the patient with heart failure.
		DR. RAMSEY:  I think in the interest of letting the panel dominate the discussion, I'd like to have you stop now.
		DR. KUBO:  Okay.
		DR. RAMSEY:  And if there are specific questions about this -- 
		DR. KUBO:  May I make just one last point in conclusion?  Just one last point.  This is a well-validated instrument, and I think you're seeing many more uptake among clinical trials community, you'll see that it's used in two other device trials, one other ongoing surgery trial, and one other pharma trial, a big pharma company, so it is gaining acceptance, although this was the first time it was used in our trial.
		DR. DeMETS:  Can I ask a question about - which is why I wanted to ask it in the first place?
		DR. RAMSEY:  Yes, please.
		DR. DeMETS:  When I look at the primary endpoint in a trial that's not blinded, the issue that goes through my mind right away is potential for bias, and all device - well, nearly all device trials have this issue.  Mortality, I assume we can get that straight.  The other two components, I have to ask the question.  So my question - the reason I raised it earlier in the day, I wanted to understand not that the assessment is done in a blinded and unbiased - it's the source of the data, the physician or whoever is filling out the data that you interpret - tell me is there any way that bias - I can be comfortable that there's no bias in the way that it's filled out?
		DR. KUBO:  Yes.  With this instrument, we do not eliminate patient bias, because the patient is not blinded, but the assessor is blinded, because they only see the results of the questionnaire.  They don't see the patients at all, so the value of the instrument is that it reduces one source of bias that could be done in an unblinded trial.
		DR. DeMETS:  But you have to accept that there is still potential bias at the source.
		DR. KUBO:  Correct, at the patient, yes.
		DR. RAMSEY:  I think there was someone - yes, please go ahead.
		DR. PINA:  Well, maybe not totally biased at the - unbiased at the source, either, because the patient is not filling the questionnaire directly, someone is administering the questionnaire, and I guess if someone has had a median sternotomy, you're not necessarily blinded later on.  However, the Kappa statistic for the original validation has fallen anywhere between .55 and .73 inter observer variability.  The correlations with some of the functional measures, although two of them are statistically significant, for me as a clinician, they don't make me comfortable, because ER is .47 for Minnesota, minus .32 for the six-minute walk, and for peak VO2 it's minus .15.
		DR. DeMETS:  I understood the answer to my question was that bias may be minimized in the evaluation, but bias cannot be ruled out at the source, so I appreciate your answer, but I think I got the answer to the question I was asking.
		DR. RAMSEY:  Okay.  Do you have a comment?  Dr. Maisel.
		DR. MAISEL:  Thank you.  Dr. Maisel.  I think what we've seen is that smart well-meaning people can interpret data in different ways.  I think what we know is that a primary endpoint for a heart failure trial should represent improvement in heart failure status, and I ask you to consider two patients.  Patient A is a patient who gets the CorCap and has no change in their heart failure status, and Patient B is a patient randomized to control, who gets a bi-ventricular device, and improves their heart failure status.  Patient A is classified as no change, Patient B, who actually had a less invasive procedure and improves, is classified as worse heart failure status, so I think that's one of the things that our panel grappled with, with regard to the primary endpoint.
		DR. RAMSEY:  One moment.  Let me just ask the panel if they have questions.
		DR. LASKEY:  Just as a follow-up to that theme, hopefully, a follow-up.  You can't run and you can't hide, so let's talk about all-cause mortality, or re-hospitalization.  And, hopefully, you can reassure me that these were adjudicated re-hospitalization for heart failure, but these are dead-on, as well.  There is no difference in these incidences of death or re-hospitalization in the two arms.  You can't run, you can't hide, you're either going to die, or you're going to wind up sick enough to get in the hospital, but there's no difference.  So how does that sit with clinical improvement?
		DR. RAMSEY:  Are you asking Acorn?
		DR. LASKEY:  Yes.
		DR. RAMSEY:  Okay.
		DR. MANN:  So I guess one way of interpreting  that question, if we withheld life-saving procedures, such as transplant or VAD, there would have been an increase in the frequency of heart failure hospitalizations, or overall hospitalizations.  We didn't see that.  
		DR. RAMSEY:  Do you have anything you'd like to add, FDA, right now?  
		DR. DeMETS:  I just want to make one comment for my colleagues. I just want to say that I really appreciate the fact this trial was randomized, tried their best to adhere to the intention to treat principle, and as - struggled, as we always do, but also tried to develop a more clinical-oriented outcome.  My years sitting on device panels, is I had outcomes which were structural, or intermediate, or functional, but didn't necessarily translate into clinical, so I really want to say as a reviewer, I appreciate the attempt and the adherence, and all the fuss about how the imputation is, because you want to stick to the intention to treat principle, so I think we shouldn't lose sight of that.
		DR. RAMSEY:  Any comments?  Dr. Crittenden?
		DR. CRITTENDEN:  Just out of curiosity, why do the investigators in the Acorn trial think that the  EFs didn't improve?  I'm having a problem kind of understanding that, as to why that - I would have thought that would have improved.  Any insight on that?
		DR. BOLLING:  Give me a moment, we're going to put up some data.  This slide shows comparative changes in ejection fraction in patients enrolled in pharmacologic studies, namely, SOLVED and the ANZ trial, the Australia-New Zealand trial with Carvedidol, changes in EF with CRT, and then lastly, to the far right, changes in ejection fraction with CorCap MVR.  As shown on the right hand panel, there was a decrease in the ejection fraction in the CorCap MVR that was not clinically significant - pardon me, in the control group, whereas, there was improvement in the ejection fraction in the treatment group.  And this was mirrored by similar changes in the no-MVR group.  These changes overall did not reach statistical significance.  If you look at the aggregate changes, as I've said in my earlier comments, I think it's difficult when you have a trial and in which you're doing a surgical procedure in two-thirds of the patients which will leave the patient with a lower ejection fraction, so when you - in MR the ejection fraction is falsely high because there is a - it was going backwards into the left atrium.  When you acutely cut that off by doing a mitral valve repair, or a replacement, despite how good our surgeons are today, by definition, the ejection fraction will go down a little bit.  In time, as the ventricle heals and remodels, and whatnot, there's a slight improvement in ejection fraction, so my interpretation of why we didn't see more robust changes in the ejection fraction that were statistically significant overall is that you're really looking at two different things over time.  And as the slide shows, there was an improvement in the ejection fraction, just the aggregate results were not statistically significant; although, at the final endpoint at 12 months, there was a trend towards improvement.  We're not allowed to say that, the intention was to look at the changes in ejection fraction over time, and when we did that analysis, it wasn't significant.
		DR. CRITTENDEN:  It seems to me, and Dr. Acker and Bolling can comment that one of the advantages of mitral valve repair is that you don't get that detriment early on, or even later on in ejection fraction.  I guess it'll be different in different patients, depending on their preoperative  EF, but I always thought the teaching was that now -that's why we want to repair more valves, because you'll get a better - you'll get improvement in the LV function much earlier.  And I would bet that even in patients who have had mitral valve replacement, I bet the majority of those probably had preservation of sub-valve or apparatus, which is what we try and tend to do if you replace the valve.
		DR. BOLLING:  You're absolutely correct.  In this trial, the patients who did get mitral valve replacement had preservation of their sub-valve or apparatus, but the numbers were too small to compare between the two groups.  But you're absolutely right, that in mitral valve repair we see much better preservation, both short-term and long-term of left ventricular ejection fraction, remodeling, improved contractility.  But what Dr. Mann is talking about, and what you and I both see in a patient who even we do a mitral valve repair on, is that when we look at that patient, their ejection fraction is falsely or pseudo elevated as us looking at it.  So if their ejection fraction appears to be 30, it's actually 20 forward flow ejection fraction, and we fix the mitral valve very nicely, and we unmask their real ejection fraction, which looks like it's falling, and it actually does take time.  And most of the big studies, not just the one that Dr. Grossi referred to, but in other studies of our patients who had myopathy and mitral valve repair, in the original cohort 10-12 years ago, we saw their ejection fractions fall in the first three to six months, and it was not until 12, or even 18, or 24 months that we saw then that eventual recovery, so you're exactly right.
		DR. CRITTENDEN:  In both of your practices, I was looking at the enrollment for both of your sites.  Most of the patients that you all enrolled were in the mitral valve cohort.  Is there any particular reason why that was?  You said the decision for surgery was made as a committee, not just by you guys who have, I'm sure, mitral valve practices.
		DR. BOLLING:  Yes, I can comment on my practice.  My practice encompasses almost all mitral valve patients, so the patients who are coming through almost all come to us with mitral regurgitation, and so we -- I, personally, just don't see that type of patient who doesn't have mitral regurgitation, but that's just my practice.  Mike can comment on his.
		DR. ACKER:  Similar answer, large practice dealing with functional MR.  We did do one patient that was CorCap alone, but again, I think it reflects the geographical differences and the enthusiasm one accepts that mitral valve surgery should be done for secondary MR.  If you look through that list of sites, there are also sites that did no mitral valve surgery, and exclusively, or almost exclusively implanted CorCap alone based on a bias towards, as we don't know, is correcting MR really good for functional MR.
		Dr. CRITTENDEN:  So the rings that are currently being - that are FDA approved for mitral valve regurgitation also talk about their ability to induce reverse remodeling.  I think Dr. Bolling has one that makes similar claims, so the question is how do you tell the difference between what CorCap does, and what a ring will do, and is that an important distinction?
		DR. BOLLING:  Well, in this trial, that particular ring that you were referring to was not utilized, was not on the market at that point in time.  And, in fact, this was a wide smattering of rings that were used on clinical judgment, and there may have - being some rings that are particularly better than others; but, of course, this is a randomized trial, and that came out in the wash, so I think that we would like to say that the reverse remodeling was from that one - eliminating that MR, and then the device.
		DR. CRITTENDEN:  So is it passive constraint or eliminating the MR?
		DR. ACKER:  We don't know, because we've never done a controlled study of elimination of MR, but I do want to speak to the fact that this makes theoretical sense to add a ventricular solution to a ventricular problem.  When you put a ring in, you're assuming that annular reshaping is going to have a downstream affect on reverse of ventricular remodeling.  May or may not be true, we have not done the pivotal trial, but we do know that in the end, what we need to do is affect the ventricle itself.  And here we had the ability, not only to eliminate MR, but actually to impact on the ventricle, and we did see signals of reverse remodeling, even in the mitral valve subgroup, which were decreased left ventricular end-diastolic volume, decrease end-systolic volume, and improvement in sphericity.  
		DR. RAMSEY:  I'd like to give the FDA a chance, because they've been pleasantly, and patiently waiting to jump in here, if you have any comments you'd like to make, as well.
		DR. PINA:  Yes, thank you.  I think Dr. Crittenden, you've been very good at pointing this out, and I think, in fact, in due - good faith to the excellent surgeons at these sites who do mitral valve repair or replacement routinely, 50 percent of the MVR stratum patients were, in fact, enrolled in five of the 29 sites.  If we look at three top enrolling sites, 51 of the MVR procedures were done there with seven in the no-MVR procedure.  And in contrast, 37 percent of the no-MVR patients were enrolled in three out of the 29 sites, which may be part of the expertise. 
		We also want to show one additional slide, if I may.  So we look at LV mass as heart failure cardiologists as beneficial - reduction in LV mass as a beneficial part of what we would like to see in reverse remodeling.  And I think it shows very nicely here that the MVR really took care of a lot of the reduction in LV mass, but if you look at the no-MVR group, the control group seemed to slightly improve their LV mass even greater, so just a couple of comments.
		DR. RAMSEY:  Go ahead.
		DR. SACKNER-BERNSTEIN:  Could Acorn put up their last slide showing the EF changes once again?  The reason I'm bringing up this slide is that as I look at this, and please tell me if I'm interpreting this incorrectly, and I try to imagine what the mean effect is in the CorCap group, and the control group over there, and the two pairs of bars to the right - I would estimate that there is a Delta EF of at least three percentage points reflected by this graph; yet, the results that you presented numerically was less than one percentage point.  Could you explain to me what I'm seeing wrong here?
		DR. MANN:  I'm sorry, Jonathan.  Can you just repeat the question?
		DR. SACKNER-BERNSTEIN:  The graph makes it look like the difference - the treatment effect of CorCap is at least a three percentage point difference in EF; whereas, the numbers that represented by Acorn in their presentation first thing this morning show that it was less than one point.
		DR. MANN:  So the difference is that the data that were presented this morning show the longitudinal regression, and that's shown here.  That's what we presented, and that was pre-specified, and that's why we showed that.  		DR. SACKNER-BERNSTEIN:  This is a 12-month specifically.
		DR. MANN:  Yes.
		DR. SACKNER-BERNSTEIN:  Thank you.  
		DR. LASKEY:  A quick question for maybe Mike Acker or the statistician.  Given what you said about the variability in use of mitral valve surgery at these sites, is it at all possible that the association between treatment and outcome is confounded by site?
		DR. ACKER:  I think we've looked at that, and I don't believe there was any site difference.  That was looked at very closely.  Correct me if I'm wrong.  Yes, there was no difference, and that was looked at.
		DR. RAMSEY:  Does FDA agree with that?
		DR. THOMPSON:  As far as I know, yes, I agree.
		DR. RAMSEY:  I think we are at a point where we should take a break. It's a bit early, but I think we should take a 15-minute break, and we'll reconvene - well, let's reconvene at 3:00.  And we will, again, start up with the question and answer session, and if there are none, then we will move on to the next phase - discussion, yes.
(Whereupon, the proceedings went off the record at 2:43:38 p.m., and went back on the record at  3:00:09 p.m.)
		DR. RAMSEY:  Let's go ahead and resume the meeting, please.  We're going to continue the open committee discussion, and I have a couple of issues that were brought to me, and I think will help this last part go smoothly.
		First, a request to both parties that we really don't want people coming up to the podium, just go ahead and respond from your seat.  And, also, although I think you've done a very good job of this, in general, we'd like very short, crisp answers.  And kind of one at a time answers, so if Acorn, for example, has a response, then we'd like to give -- from one individual, we'd like FDA to have a chance to respond right then and there, and then we can go back if there are others from Acorn who want to respond, so I'm going to try and do it that way.  And I promise, I want everyone to have a chance to present their side, so I won't leave anyone out.
		I believe the panel has a couple of more questions, perhaps, of the sponsor and FDA, and then we'll probably spend some time discussing among ourselves our thoughts.  So let me again turn it back to the panel, and ask the panel members if they have any questions for the FDA or the sponsor.
		DR. CRITTENDEN:  I have a question for the FDA.  We heard Dr. Kubo - I may not be saying his name correctly - present what he thought was validation for  the core estimations, core lab estimations of New York Heart Association class.  You all didn't have a chance to rebut or respond to that.  I'd like to hear your response, because that sounded like that was a key issue of unreadiness on the FDA, exactly what the core lab NYHA classification meant.  And then, too, if you could respond to the question about the unreadiness about multiple imputations.
		DR. PINA:  Thank you for letting us talk about that again.  I think we still struggled with what is the core lab actually measuring.  We appreciate the diligence of trying to come up with a questionnaire that is as unbiased as possible, trying to take out the bias of the operator that's looking at that.  But we continued to be concerned with the fact that the core lab is over-assessing as far as New York Heart classification, and placing the patients at the site - I mean, it's not perfect.  Certainly, site-assessment of New York Heart class is not perfect, but we all kind of put together some questions, taking a look at the patient, kind of putting it together.  These, to me, seem to be clinically very different assessments.
		DR. CRITTENDEN:  If any collectors were not trained by the sponsor at the sites, there was no specific training or inter reliability studies done at the sites?
		DR. PINA:  The validation study that Dr. Kubo published had validated the questionnaire in a separate group of 116 patients.  It is not clear to me, personally, whether the core lab that looked at that validation was the same as the core lab validators that looked at this one.  And I'll let Acorn answer about the training of the individuals who actually administered the core lab measures.
		DR. MANN:  So first we can answer yes, affirmatively to it was the same group that did the paper, that did this.  And I also wanted to clarify one other issue.  There was a blinded assessor at each site who did fill out the questionnaire.  That person had no idea what the patient had had.  Furthermore, all interviews were conducted with the clothes on so that no median sternotomy would be influenced.  Nonetheless, we can't exclude individual patient bias, but I think I'd like to emphasize that every attempt was made to do this in as blinded a fashion as humanly possible.  I think Dr. Piantadosi wanted to also comment on the relative differences between the core and the site, which were the same between the different classes.  
		DR. RAMSEY:  Steve, before you jump in, does FDA have anything they want to respond at the moment?  Go ahead, Steve.
		DR. PIANTADOSI:  Thank you, Dr. Ramsey.  I just wanted to re-emphasize, in a sense, one obvious point, and one not so obvious.  The obvious point is that this is a randomized trial, and that whatever differences we may think are present, are expected to be present in both groups, exception, of course, being the potential for some small residual bias because of the patient's self-assessment.
		The relative difference, though, in the treatment effects, depending on which measure you use, or which level within a given measure site or core are the same, so although there seems to be a lot of concern about exactly what the correct classification is for individuals, given the fact that the relative degree of improvement is in the proportional odds model the same, I think that these concerns really are not substantive.
		DR. RAMSEY:  Yes.
		DR. ZUCKERMAN:  Well, we would have concerns with Dr. Piantadosi's last comment because with New York Heart Association you're rating one through four.  There's a ceiling effect, can't get worse than four, and these problems aren't necessarily going to manifest themselves equally between both groups.
		DR. RAMSEY:  More questions from the panel?
		DR. SACKNER-BERNSTEIN:  Dr. Ramsey had earlier asked a question about the NYHA class assessed at the end of the trial, the common closing date.  And Dr. Starling, you showed data in graphical form that you had shown in your preliminary presentation that showed what the NYHA class was at the conclusion of the trial.  I think it would be useful for us to know what the change in New York Heart Association class was over the course of the trial, and what was the proportion of patients whose NYHA class improved, worsened, when you were showing it relative to the patients who had a major cardiac procedure, and those patients who died during the procedure, so we can see where everybody fell in in terms of their -- what bin they fell into by the end of the trial; improved, worsened, the same NYHA, major cardiac procedure, and death.
		DR. STARLING:  Thank you, Jonathan.  I'm not sure that I have all the information at my fingertips, but we'll attempt to pull it up.  What I did show on the presentation, which was in my last slide, clinically important benefits with respect to functional class, and what I stated was that 38 percent improved by one or more NYHA class, versus 27 percent in control.	
		DR. RAMSEY:  If FDA had the information, I'm sure we'd be happy to see that.  I don't know if we do. A third option is we could ask another question while we're gathering the information.
		DR. BECKER:  Dr. Ramsey, this is Karen Becker.  I think we need a little more time to find that data.
		DR. RAMSEY:  Well, let's hold on for a moment and see if the panel has another question.
		DR. LASKEY:  Am I allowed to ask to see the data that Dr. Acker put up, he put up the two bar graphs of the perioperative mortality.  Is that data that the agency has seen yet, or is that something that you alluded to, you haven't seen that?
		DR. RAMSEY:  I believe you have seen that, yes.
		DR. LASKEY:  Could we just see that again, and perhaps we can get a more - or just a composite 30-day mortality rate now with those two groups.  So does someone want to give me a current perioperative mortality rate with confidence intervals?
		DR. RAMSEY:  How do you mean current?
		DR. LASKEY:  Well, yes, add these up, going to have one additional death and 33 implants, three - so we have four deaths, and 51 implants.  What is that rate, and what is that precision?  Getting back to Jonathan's, what's the upper bound for the perioperative mortality?  Easy enough to do.
		DR. RAMSEY:  Didn't you have that data?  Go ahead and show it, please. 
		DR. LASKEY:  Thank you.  
		DR. RAMSEY:  Again, any questions from consumer or industry reps?  Happy to have them.
		DR. HUGHES:  Okay. I'll ask a question to fill a little bit of time.  Just a little point of clarification I'd like to have, and that's with regards to the data being divided into control and CorCap, and then from there, mitral valve repair, mitral valve replacement, non-MVR.  Does it matter - I assume it doesn't, but tell me why it doesn't matter in terms of the results whether we're talking about mechanical valves or bio valves?  Is that accounted for in the statistical make-up, the data analysis at all?
		DR. ACKER:  Excuse me, Michael Acker.  There is a lot of different types of rings, and a lot of different valves used, so we have to lump it together.  I can tell you there is no difference in mortality between replacement or repair.  The mortality actually was 1.6 overall, and there was zero death in the few patients that actually had replacement compared to control.  And we saw no differences - again, we weren't powered to do that between types of rings, or types of valves.
		DR. HUGHES:  And I take it the same holds true with regards to the change in size of the heart over time?
		DR. ACKER:  Yes, that is true.  There was no difference between evidence of reverse remodeling, whether you repaired or replaced the mitral valve.  You can put up Slide 211, that might give you some more detail.  Go ahead.  So you can see a lot of different types of rings were used here.  And, again, there was no difference among these groups.
		DR. HUGHES:  Okay.  Thank you.
		DR. MANN:  I think we're prepared to respond to the New York Heart question.  
		DR. RAMSEY:  Did FDA have a comment first before we get to that response?
		DR. ZUCKERMAN:  No.
		DR. RAMSEY:  Okay.  Go ahead.
		DR. MANN:  We have the slide -- 
		dR. RAMSEY:  It's hard to make them on the fly, I understand.
		DR. MANN:  We got it done.  Okay.  So this is the change in the core lab NYHA classification admitting patients who died, major cardiac procedures considered as NYHA, Class IV, showing the percent that improved, remained the same, or worsened.
		DR. SACKNER-BERNSTEIN:  So if a patient had a major cardiac procedure who was NYHA Class IV at baseline - I know there weren't many of those - but that would mean they would be considered the same in this analysis.  Were there any of those, any Class IV patients at baseline in procedure.  I know in the rank order they would be worse in the overall score.  I'm just trying to get a sense of how -- I guess this is as good as we're going to get.  Okay.
		DR. ACKER:  We tried to avoid Class IV patients throughout the trial.
		DR. RAMSEY:  Did you have a comment?
		DR. ZUCKERMAN:  The comment was made that we tried to avoid Class IV patients throughout the trial, but I would go back to the correlation slide again that we showed.  Site Class III we agree they were enrolling a Class III patient population, but yet, somehow the core lab was showing roughly 50 percent of patients as Class IV.  And it just, again, underlines how the clinical gestalt just doesn't seem to be correlating with this concept of core lab NYHA.
		DR. RAMSEY:  Do you -- before we let another FDA person chime in, I'm again working for balance here - does Acorn want to respond?
		DR. MANN:  Again, I would go back to what Dr. Piantadosi said, is that the relative differences - any instrument I think you're going to have differences in absolute numbers, but the relative differences between the core and the site remain consistent.  And as we have alluded to, I think at times the New York Heart is imperfect, has tremendous inter- and intra-observer variability, whereas, we believe that there's less with the core measurement.
		DR. RAMSEY:  FDA, did you have one more thing you want to say?
		DR. THOMPSON:  Actually, I have two.  I don't believe the relative difference between CorCap and control was the same in site NYHA versus core lab NYHA.  The percentage improved in the site, was actually reversed, albeit, not that much, so the difference in site - there was a greater percentage of control patients who improved than CorCap patients, and in core lab NYHA that percentage was worsened.  And one other point I wanted to make regarding Acorn's choice of categorizing patients who had major cardiac procedures as Class IV NYHA at the final follow-up; one of the tables I had presented before showed a total of 31 patients who were counted as having additional major cardiac procedures in the database, but on the last available core lab NYHA, they were not Class IV.
		In fact, what was reported to us in the submission was that any patient who had a major cardiac procedure did not have a final NYHA assessment, and so to figure out what those would have been in my own assessment, I used the last available in the data set.  And if you look at the first row, there's a total of 31 patients who had major cardiac procedures, but were not Class IV on the last available core lab NYHA in the data set, and it's divided 20 and 11 between control and CorCap.
		DR. RAMSEY:  Okay.  Go ahead.
		DR. RUBIN:  I'd like to again point out what Steve Piantadosi pointed out maybe about an hour ago, that these analyses are stratifying on an outcome variable and they're invalid.  They violate the intention to treat principle, they violate other principles.  They're just invalid, they're stratifying on an outcome variable.
		DR. SACKNER-BERNSTEIN:  Well, along those lines, could I make a comment?
		DR. RAMSEY:  One second, please.  Go ahead.
		DR. SACKNER-BERNSTEIN:  I would agree with that statement, that using an outcome variable is fraught with all sorts of problems.  And it's one of the things that concerns me about the imputation model, if I understand it correctly, because the imputation model appears to include amongst its 10 variables that are put in the initial model, such things as death later, NYHA class at 12 months, so by the very nature of trying to impute a baseline parameter, you're using post randomization data.  And, to me, that seems like it should be a sign of caution about the applicability of the model.
		DR. RAMSEY:  I'm going to go to FDA, and then I will go back to you.  Do you want to have a response?
		DR. THOMPSON:  I can respond to that, what I heard - I didn't hear the whole thing because I was having a conversation, but are you referring to including post baseline variables in the imputation model versus - even with just baseline variables, the result is essentially the same, so it didn't affect the numerical result, in percentages, it didn't affect that much either.
		DR. RAMSEY:  Go ahead.
		DR. RUBIN:  That's a very good question.  And, in fact, that's why I prefer to do each treatment arm separately, because the outcome variable - it's a different outcome variable with outcome of your treatment, outcome of your control.  It's completely valid if you're doing it separately by treatment arm, and those were models three and four, as being presented.  And if you don't do it, I guess, there's a model one that did it all together; that, in fact, it's valid in a frequentist sense because it pulls the data towards the null, if you do it - you're treating the outcome under treatment, or the outcome under control as the same variable, which it's not, and so the imputations are pulling the data slightly towards the null, which in a strange frequentist sense is always a valid thing to do.  It's conservative, but I don't like to do it that way, and so that's why imputation models three and four have complete separate imputation for treatment arm, control arm to the CorCap arm, to control.  Excellent question.
		DR. SACKNER-BERNSTEIN:  As a follow-up, maybe you can explain to me then what the basis is for creating a different model for each treatment group.  In my limited view, limited background in statistics, it would seem to me that what you would then be doing is taking a relatively modest size trial, and taking any of these parameters which might be, by chance, slightly different between groups, and using a technique that would put one at risk of amplifying those differences in terms of how you do the imputation, because you're creating a different model for each treatment group.
		DR. RUBIN:  Well, it can't amplify differences that aren't there.  What it can lead to is increased variability in the imputation relative to a model that, if there were more sample size would be more precise.  And, in fact, there is a minor technical issue, that if you're doing it at baseline, that you can create differences in covariate distributions.  There's a restriction that by the randomization, the covariate distribution should be the same in both randomized arms.  And that's not being implied by the imputation as you're doing it, if you've done it completely independently in both arms, so as a matter of fact, what you have to do at the end of all the imputation is actually not do a check, but actually do a, I guess, really an important sampling of the imputed values to pull it back towards the null on the covariate values.  It's a very insightful question, and there is an additional step that has to be done to do it correctly, that was in this model four, that's being developed for CDC.  And it's not, for example, in any of the SAS routines, so the SAS routines are valid, but they tend to pull things towards the null hypothesis.  Eventually, SAS will do it fully right, but they're not there yet.
		DR. RAMSEY:  I think FDA wanted to respond.  Go ahead.
		DR. HILLEBRENNER:  Yes, I apologize.  I think this is a response to an earlier statement during this discussion regarding the over-estimation of CorCap with respect to site, and the idea that using randomization, you would expect this to be similar between the control and the CorCap groups.  First, I would like to say that I still think that brings the question of what is core lab measuring, but if we want to look specifically at the patient groups, Ileana Pina is going to refer to that.
		DR. PINA:  If I can have that slide up, please.  I had previously shown you the 126 patients that had both site and core lab.  Here they are divided out by control group, where you can see that out of 49 patients classified as Class III, nearly 50 percent became Class IV on the core lab.  And then I'll show you in the next slide, if I can have the next slide, this is the treatment group where the number of patients who were Class III and molded into Class IV were higher by percentage than in the previous slide we just showed for the control, so they're not exactly the same.
		DR. RAMSEY:  Any more questions for Acorn or the FDA?  Otherwise, I'd like the panel to sort of turn to itself and perhaps have a little discussion among ourselves about our thoughts at this point, and see if we have a consensus about questions or issues, or just general opinions.  
		DR. LASKEY:  So a general backup-type question - heart failure in the United States, huge problem, need to do something.  The vast majority of heart failure in the United States is related to coronary heart disease.  We're here evaluating a patient population who were devoid of coronary heart  disease.  How relevant is this whole exercise?  It's just a rhetorical question, but something for us to grapple with if we vote to move ahead, or to modify, or to whatever we're going to decide, but these patients that we're struggling with to define may be entirely different than the ones who occupy the vast majority of heart failure in the United States.  That's one of the key issues that I've been struggling with from the beginning.  And I'm just - whether it's worthwhile to pursue it or not - would like to know whether these discussions occurred with the company, between the company and the FDA, and why they decided to go with a "minority" population, rather than the killer in the United States today.
		DR. RAMSEY:  It seems to me that the device itself sort of precludes ischemic cardiomyopathy or the group who could benefit from revascularization, so I think your point is well taken.  That said, I think they picked the patient population based on the characteristics of the device, and I feel comfortable, personally, that they've not tried to ease this into the larger population.
		DR. LASKEY:  I understand that, and there's no answer, and this is what's been done, has been done, and is a credit to Acorn and the agency.  But the other thing that I'm grappling with is the role and the influence of mitral valve surgery, which in the setting of dilated cardiomyopathy is always a nightmare in terms of which is the chicken, and which is the egg, and is heart muscle leading to regurgitation, or is it regurgitation which has just gone out of the barn, and is now end-stage heart failure due to that?  And two-thirds of this population had a mitral valve intervention, which is - when successful, and it generally is, will reduce ventricular volumes, will reduce rejection fraction, will increase ejection fraction, will improve sphericity, and all these other things that are being ascribed to the device, rather than to the penetrating influence of mitral valve repair, so I'm just grappling with that, as well.
		DR. RAMSEY:  I want to add my comment to that, because it is hard for me to tease out the impact of the mitral valve procedure from the CorCap device, and I'm trying to decide whether they're additive, or synergistic, or - what do people here on the panel think about that?
		DR. CRITTENDEN:  It would be my bias that it's more the repair than the replacement, but I think the point that one of the surgeons made was that this is a ventricular problem, just like you were just saying, and if you look at risk factors for failure of repairs over time, especially patients in this particular group who fail more than others, you look at a patient who has a mixominous disease, they don't fail as much as patients like these who have functional or dilated cardiomyopathy.  So a lot of surgeons are looking for the magic bullet to protect the ventricle because we know that they're going to dilate over time.
		DR. SACKNER-BERNSTEIN:  Well, I agree with that concern about trying to understand how the procedure is interrelated, and I think at first glance, you can look at the data and say - one could say.  I'm not saying this would be my interpretation, but one could say wow, look at how the CorCap led to a -- the CorCap MVR group had a lower perioperative mortality, maybe there's some interrelationship that makes it safer.  But I would caution against doing that, because much of the mortality in the no-MVR group occurred in patients who underwent the procedure without cardiopulmonary bypass, and once they made that change, the risk did seem to fall down into a similar range.
		With that said, of course, that brings back the question of the overall risk of the procedure with the confidence intervals as were brought up for both 30-day mortality and the ones that I estimated for overall mortality that leave the procedure risk to be estimated potentially in a range that would seem rather high.
		DR. RAMSEY:  What do people think about the imputation methods?  I mean, on the one hand - and this is obviously one of the core issues that has been discussed - on the one hand I think we have the inventor of multiple imputation, who I think has done a solid job, doing the best with a difficult situation.  On the other hand, it's an extraordinary - at least to my mind - amount of data that needed to be imputed.  What do people think?
		DR. HUGHES:  I have to say -- 
		DR. RAMSEY:  Allen, did you have a comment?  I'm sorry.
		DR. HUGHES:  Okay.  I guess I was just going to comment with regards to it being analogous to something that we do in School of Business, School of Management, and that's data mining.  What you're trying to do is - I guess what I'm doing is I'm really thinking more about the focused cohort issue, rather than missing data.  But nonetheless, what I had on my mind was that you end up scouring the data looking at what you've already put together for a different purpose, and now you're scouring it for some other sets of purposes.  That's one of the things that I've seen going on here.  And I think with regards to what I say to my students in the School of Business, is that once you come up with a new insight after looking at the data from different perspectives, you sit back and you ask yourself the question - well, this insight that I see here from doing this data mining, does it make sense?  Is it something that makes sense to me now that I've done this procedure?  You can't really say that in this kind of forum with regards to medical device risk management; and so, therefore, I guess what I'm getting at is once you've found a different perspective, it seems to me that you have to take some time and actually collect the data prospectively to check it out for sure.
		DR. RAMSEY:  Go ahead.
		DR. DeMETS:  I was going to try to answer your question about the imputation, and maybe I'll go a roundabout way of doing it.  So we have, in some sense, many design aspects which are favorable and good, it's randomized, tried to adhere to the intention to treat principle.  And as in many device trials, or any trials where you have non-mortality or non-event outcomes, you try to measure things, and you have missing data, and so you have to find a way to deal with it.  If you didn't have your regulatory hat on, and weren't worried about the .05 level, would you have come to the conclusion that the imputations tell you that this stuff is pretty robust?  Doesn't matter which model you use, whether you use downstream variables or not, which I didn't personally recommend, but even if you did it, you'd get a pretty robust answer.  So in that sense as I read all of the documents, I was, perhaps, less troubled by the imputation part than was earlier.  But where I was stuck, and am still stuck, is on the nature of the primary outcome.
		In Trials 101, you sort of talk about being able to ascertain all patients in an unbiased way.  Mortality, as I said earlier, is pretty straightforward, but the other two outcomes, I have been thinking all day long where could bias have influenced this?  It's a relatively small study, 300 patients.  The percentages that are presented, about 10 to 15 patients difference one side of the table, so it's not large numbers of patients.  And I'm trying to - maybe someone on the panel can help me to be assured, reassured that the potential bias couldn't affect just enough patients to make this difference there.  Okay.  So I'm troubled by this outcome.  Where's help?  So I retreated to the outcome which I'm also familiar with in trials, death and hospitalization, and you can - you don't have heart failure hospitalization, we just say hospitalization.  And there, I see no difference.  I'm not worried about P values.  I'm just looking for qualitative help, and I don't get it there.  And then I said well, okay, live longer, feel better, is okay.  And the feel better part, the quality of life stuff, there's a positive trend but it's, at least to my experience in these quality of life instruments, it's a small difference.  And then I retreated even further into the woods and looked at ejection fraction and those kind of things, and you see small differences there.  So I didn't get the help I wanted, given that I'm troubled by the potential - and I say it's a potential. I can't prove it either way, but that's - so the imputation part for all those reasons, to me, is not the key issue.
		DR. RAMSEY:  That's a great comment.
		DR. SACKNER-BERNSTEIN:  Hardly will I be able to say something as clear as that, but I am still troubled by the missing at random assumption, which as I understand the imputation methodology is a crucial part of understanding its applicability.  And I think there are enough reasons to suspect that we might be able to make the assumptions that are necessary for that missing at random assumption to be valid for this data set.
		DR. RAMSEY:  Did you have a comment?  Your finger is poised.
		MS. WALKER:  Yes.  Interesting discussion as we're bouncing this back and forth, and listening to the various thoughts on this.  It is often difficult when we are designing studies, and then when you get results and analyze data, especially for difficult clinical conditions, or conditions where there are few options for - even if it's a small patient subset. I would like to ask the panel a question, actually, as far as challenging to think a little bit about what opportunities, or what patient population there is in this that may see a benefit, I mean, to the point about mitral valve repair, and to the point about ischemic.  Is there a patient population that you would expect, based on what you see, that would potentially benefit from this therapy?
		DR. RAMSEY:  I'm going to give the non-statistical answer, which - I mean, I think the focused cohort is the - as I think both parties agree, is the most promising place.  That said, there's still a worry for a Type I error, saying that there's an effect when, in fact, there isn't.  And that seems clear to me, as you broaden out of that focused cohort, I become more and more uneasy, and can't say with regards to the repair arm or not whether I'm certain that I -- but that will be my opinion.  I hope others will chime in.
		DR. SACKNER-BERNSTEIN:  I think that's an excellent question. I think that is part of why the focused cohort is so important, in my view, is that it helps to identify a group that would seem to have the best response, but it would be hard for me to say that I'd be comfortable concluding that that is a subgroup where something is proven, and I don't think anybody from either side has asserted that, partly because, on a simplistic basis, if you're designing a statistical plan to try to identify a group who responds best, you should be able to identify a group who responds best.  It's almost a self-fulfilling prophecy, so the challenge would be to figure out a validation strategy which would require you to go to another data source, such as another trial.
		DR. LASKEY:  It seems to me you do the parent trial, and then you go look at groups which benefit, and so forth, that are hypothesis generating, and pursue that.  I'm not sure we've settled the issue of this integrity of the parent trial; and, therefore, looking at choosing an end-systolic volume index based criteria could be as valid as any other criteria, so I'm concerned about going back to the focus trial without settling on does the parent trial - what message does the parent trial convey here?  And again, I would only add commentary to what Dr. DeMets has said, which is this is what we're struggling with, and clinicians when confronted with conflicting data turn anywhere, he goes back into the woods.  And while I look at mortality and hospitalization, and neither of us can see a signal here.
		DR. RAMSEY:  I'll just add to that.  I mean, the other measures which we haven't talked about much today, and perhaps the rest of the panel can respond, is the six-minute walk, peak VO2, and SF-36.  Now these are secondary endpoints.  Oh, also the BNP, which three of those four favor the control arm, and I realize there's missing data in all of those endpoints.  But, on the other hand, those are, perhaps, with the exception of the SF-36, somewhat less subject to bias.  And I wondered what others thought about those in the context of this issue that we just feel this unease with the primary endpoint - should I discount those, or should I keep those in my pocket while I'm thinking about this?
		DR. LASKEY:  I think we shouldn't forget that.  We should come back to it, but I'm struck by the "placebo" response here.  I cannot look passed that, that it's an improvement of one in three responds in the treatment, and one in four in the placebo and control.  Just always a lesson here from these trials in heart failure what the response is in the comparator arm; and, therefore, I don't - there doesn't appear to be that much difference.  As Dr. DeMets says, you can move five patients from one to the other and see it disappear.
		DR. RAMSEY:  Yes. I was thinking that those measures with the exception of SF-36 that I mentioned, might be less influenced by that effect, but I agree, you have to think of it all together.
		DR. SACKNER-BERNSTEIN:  In terms of the effect of those measures on any sort of bias, I think that most would agree that BNP is probably not something that can be controlled very easily by a patient's mindset.  I think a six-minute walk distance is something that could be influenced to a degree by a patient's mindset.  VO2 max, since it was done through a core lab, I'm less concerned about that because there are measures that can be used as quality control, and even though we haven't seen that, I know Dr. Pina, who knows much more about this than anybody on the panel knows how to look at this, and she double checked a core lab who's also going to be focused on this very carefully, so I imagine they looked at things such as VO2 at anaerobic threshold, which is a way to get away from someone's bias, how hard they're working.  They've looked to make sure the tests are maximal, so I think that your statement about them being less biasable by a patient's mindset is one that I would agree with.
		DR. SACKNER-BERNSTEIN:  I think it's interesting to look back from the perspective that Dr. Laskey brought up about the integrity, as he put it the integrity of the parent trial. I have a concern about the NYHA core lab methodology that hasn't been addressed, thus far.  This is a methodology that I believe is one that does minimize bias, and does add consistency.  It seems that it should. I agree with what's been presented, that doctors ask about this stuff in very different ways, and so consistency would be a good thing.  But I think it's important to understand that any new approach to any measurement typically needs a model developed in one population, and validated in another.  You wouldn't use the same population for two purposes.
		This methodology has - its validation population seems, to me, to be the same population of patients for whom it was used in the trial; and, therefore, I think it's hard to understand how one can be allowed to use the same patients both to validate the model, and then to utilize the instrument as a measure of efficacy of an intervention, so I have a problem with that.
		And I also think it's important to recognize that the studies that were done, although they were very rigorous, were cross-sectional, and not longitudinal, so as people talk about this methodology as a core lab NYHA correlating with worsening status, that's from the perspective of a cross-sectional population assay, not looking at how well it tracks with changes over time.  So one of the things I could do is I could put you, Dr. DeMets, on the spot again, and say if you have a methodology that say - let's just assume that imputation worked perfectly, just to take that out of the equation for a moment, and you had a methodology like core lab NYHA, that in a good scenario here say was 60 percent accurate.  There are some estimates from the initial data that suggests it might be worse than that, but if it's 60 percent accurate at time point one baseline, and 60 percent accurate at time point two, what's the best accuracy you could have to be detecting a difference in NYHA between times one and two?  I would think it would be less than 60 percent in all reasonable estimates.
		DR. DeMETS:  It's not likely to be better than that.
		DR. SACKNER-BERNSTEIN:  So in that case, that's another reason why I think that the NYHA classification by core lab is - there's cause for concern there as to how useful and rigorous that could be considered.
		DR. RAMSEY:  I was reminded, as you were talking, those are excellent comments, that we are a bit over our time, and I think unless the panel would like to have more discussion among itself, I would like to move to the summation phase.  So the first group that's going to sum is the FDA, and you have 10 minutes for that summation.
		DR. TILLMAN:  Good afternoon.  My name is Donna-Bea Tillman, and I'm the Director of FDA's Office of Device Evaluation.  I would like to offer a few final thoughts about FDA's review of the Acorn CorCap PMA, and why I believe that Acorn has not provided sufficient valid scientific evidence to support approval of the CorCap device.
		FDA's mission is to protect the public health, to make sure that medical devices are safe and effective, while at the same time promoting public health by ensuring ready access to promising new technologies.  These two mandates can often appear contradictory, particularly when we are considering novel therapeutic approaches to important public health problems like we are today.
		However, when we have sound scientific trials that provide clear evidence of safety and effectiveness, this apparent contradiction does not exist.  Unfortunately, this is not the situation for the CorCap device.
		To determine that Acorn has demonstrated a reasonable assurance of effectiveness, you must find that in a significant portion of the target population the device will provide a clinically significant result.  As discussed by the members of the FDA review team, the results of the primary endpoint analysis are not interpretable, and even the secondary endpoints do not demonstrate a clinically meaningful benefit.
		To determine that Acorn has demonstrated a reasonable assurance of safety, you must find that the probable benefits to health outweigh any probable risks, and that the device does not present any unreasonable risk of illness or injury.  The safety questions raised by the Circulatory Systems Advisory Panel, for example, the perioperative mortality of 8 percent in the non-MVR cohort, are not outweighed by the uncertain benefits provided by the device.
		In recognition of the limitations of the original clinical data set, Acorn has attempted to identify a patient population in which there is a favorable risk benefit profile by conducting a post hoc analysis of the study results.  These results can only be viewed as hypothesis-generating.  Additional prospective data are necessary to demonstrate that these results are reproducible, and can be generalized to the U.S. heart failure population at-large.  Due to significant issues regarding safety and effectiveness that still remain, FDA believes that these data must be collected and evaluated in the pre-market setting. 
		Today you've also heard much discussion about the review process.  While this information is useful for painting a picture that FDA followed to reach its final decision, it should not affect your final recommendation.  That recommendation should be based on a careful analysis of the clinical trial data, including a consideration of the differences between statistically significant results and clinically significant results.
		Although the FDA review team does not believe that Acorn has presented sufficient data to demonstrate reasonable assurance of safety and effectiveness at this time, we continue to be willing to work with the company to develop additional clinical data that would be necessary to confirm the results of the focused cohort analysis.  
		I want to personally thank you for your time, your consideration, and most of all your patience.
		DR. RAMSEY:  Thank you very much.  We now have the opportunity for Acorn to present their summation, 10 minutes.  Dr. Piantadosi, I take it you have been elected.
		DR. PIANTADOSI:  Thank you, Dr. Ramsey.  Yes, I'm elected again as the beginner, and I'll make a few remarks, and then turn it over to my clinical colleagues.  		The sponsor has presented a randomized clinical trial that was designed to be responsive both to the clinical concerns about evaluating severe heart failure patients, and the methodological needs for rigor.  The primary endpoint here has been a source of much discussion, but has to be acknowledged as responsive to the needs for a clinical outcome to evaluate devices such as this.
		We are very respectful of the panel's concerns regarding interpretation of the primary.  It was fully pre-specified, and demonstrates substantial consistency in effect, regardless of how its various irregularities are resolved.  You can't explain away significant findings by invoking explanations of noise.  There is a chance for a small subjective patient-based bias in the primary, but the investigators did as much as is feasible to render it accurate.  
		Imputation is not the first choice for any outcome in a clinical trial, but when appropriate, as it appears to be here, is preferable to discarding data. In this study, the fraction of missing information is insignificant, and the outcomes are demonstrably not sensitive to the method of imputation.
		We can easily be misled by the vagaries of analyzing a host of secondary outcomes, but the simple and intuitive approach using direction in magnitude of effect is here, as usual, a reliable guide.  These secondary outcomes are almost perfectly consistent with the primary, although small in magnitude.
		Subset analyses, whether pre-planned, or post hoc, are full of danger.  This is true not only of the focused cohort analysis, but must also be applied to the other explicit subsets put forward repeatedly by FDA.  No sponsor would ever come to a panel or to FDA with a request to approve a therapy based on the kinds of exploratory analyses used by FDA to question this one, such as those that are subject to missing informative data.  Why then would such splitting of the data be appropriate for disapproval?
		In summary, we believe we have presented good quality, albeit, imperfect data, and augmentations to earlier summaries from which experts, such as this panel, can comfortably conclude that reasonable evidence is present.  We encourage you to make this therapy available for patients with heart failure.
		Now I'd like to turn to Dr. Jessup for some additional critical points.  Thank you.
		DR. RAMSEY:  You're doing well on time, a little over six minutes.
		DR. JESSUP:  Good.  I'll be brief, and then Dr. Mann is going to follow me.  
		I want to say that I agree completely with Donna-Bea Tillman that we all wrestle with making new technologies available, while providing safety to our patients.  Unfortunately, I feel compelled to say that this is a patient population that maybe hasn't really been given due insofar as the severity of their illness.  This was not a trial designed to compare CRT versus CorCap.  This was a trial in patients who were optimally medically managed that began over five years ago.  Certainly now, if we had those same patients, we'd try CRT.  It's only effective in two-thirds of patients.  We might try mitral valve repair alone, although there's no trial that's ever shown that to be effective.  There isn't even a trial to show that bypassing patients with heart failure and no angina is effective.  And yet, therapies have changed a lot.  CRT has become involved, ICDs are routinely applied in this population; and yet, at the end of the day, many clinicians here have felt compelled to say they still think this clinical composite endpoint showed that the CorCap allowed the patients to be in a better clinical situation compared to control; and, therefore, I would conclude that the risk of the surgery is outweighed by the benefit of avoiding transplant, avoiding VADs, and avoiding a deteriorating clinical status.  Thank you.  I think I'm going to be the one that's summing up.  Thank you.  
		DR. RAMSEY:  You still have more time.  If you want to say one thing quickly, you have four minutes.
		DR. PIANTADOSI:  Let me just speak to the bias question.  Though we feel the composite endpoint is vigorous statistically and clinically, I think everyone continues in their mind to break it down into its components.  They see mortality benefit that is none, they see a quibbling over core lab as far as NYHA classification, and the P values are tiny, perhaps.  But if you're going to break it down, the real issue is here, 41 percent decrease in the need for transplantation.  That is real.  This is something that if we do not give our patients, we're saying they're going to be transplanted, and that is basically a prescription for death in 10 years.  So the question is, was their bias in making that decision?  Was the investigators over 29 sites, either unconsciously or consciously, withheld transplants because of some sort of either fear of adhesions, which I tried to show you data, there is none, or some sort of unconscious promotion of this device.  And I think that is a real step, a real leap, when you're asking 29 centers that are making a decision as profound as transplant, that that was a significant bias.  So, in my mind, it is a real clinical outcome in the fact that our patients that got this device did not need transplants.
		DR. RAMSEY:  Dr. Rubin, do you want to make one more comment?
		DR. RUBIN:  I just want to make one minor comment, or maybe two, and it addresses John's question about the missing at random assumption.  I was very careful in my presentation to say it's missing at random for the comparison of treatment and control, because it was blocked in time.  It was randomized in time, block to treatment versus control, so that for comparisons of CorCap with control, there is no possible violation, that there can be time trends, you're right, but it's blocked in time, so those kind of comparisons are okay.
		I also just want to make one final comment, I think, to second Steve Piantadosi's comment, that I think that this trial maybe it was too small, but it was really done extremely carefully, and was randomized, tried to adhere to intention to treat principle as much as possible. I think that the analyses that were presented here by Acorn were generally very good, very statistically valid, and many of the analyses produced by FDA, certainly by FDA's standards, are not valid.  I mean, stratifying an outcome variable, and showing those analyses, I was really surprised to see that, because they know they're invalid, and I just don't know why they're being presented.  And just looking through dozens of P values, I think is sort of disappointing.  But, in any case, I know the decision is your's to make, but I do think that there's a lot of evidence for a need for this device, and there's very little evidence that it's unsafe.  I think most of the discussion about safety is based on lack of evidence, one way or the other.  So thank you very much for your attention.
		DR. RAMSEY:  Thank you.  We now are going to be moving to the panel deliberation and vote section of this meeting.  We have approximately one hour, if we need it, for that discussion and the vote.  Before we go on to the particulars and voting instructions, I want to ask the industry rep and consumer rep if they have any brief comments before the vote.  
		MS. WALKER:  Just a follow-on to my previous comment, as far as trying to determine exactly who would be most benefitted by this therapy.  I think that the discussion has clearly shown that there is a disagreement on everything from the validity of the scoring for heart failure scoring for NYHA criteria, whether it's a validated questionnaire or not.  It comes down to a very explicit question as to whether or not that data is even valid to be used in analyses.  I think that we need to consider, or that the voting members should consider whether or not there are any other opportunities to explore patient sub-populations, even in the recommendations or in the conditions that you might propose for this.  And keep in mind that there are labeling, there are very narrow indications that you can consider.  There are very explicit training activities.  There are some particular conditions that you may be able to put on to mitigate some of the concerns, or some of the questions that you have, so I would ask that you would please consider that, as well.
		And, also, going forward, actually, even though we could not consider that today, that there is obviously time has passed and there is data available, both from their continued access activity, and other long-term follow-up studies, that that's something that may -- that FDA may also consider when looking at labeling and taking the recommendation of the panel, as well.  Thank you.
		DR. RAMSEY:  Thank you very much.  Dr. Hughes.
		DR. HUGHES:  Okay.  Thank you very much.  First off, I want to acknowledge the other panel members for their fine work and review, and also, Acorn and the FDA for their fine work, review, insight.  And I really shouldn't feel much pressure on this as the consumer representative because I don't have a vote, so the pressure is put on the voting members.  But first, just thinking back as to who the consumer is, the patient, the public, and also by extension, the implanting physician as the learned agent, so to speak.  So it's incumbent upon all of us to look at it from that perspective, that we're also trying to give, as what was brought out, trying to give the physician another weapon in his or her arsenal for this particular therapy.  But, also, in looking at that, one of the troubling things that I came across, or that was certainly pointed out in the FDA's slides, I believe it was Slide 74, and that is that this -- that CorCap as an implant does preclude other options along the way, in particular, CABG, I believe, was pointed out.  That needs to be balanced against what was said just a few minutes ago, and certainly earlier on in the presentations, and that is what I would call avoidable risk, avoidable consequences; in particular, that being heart replacement - well, heart transplant is what I'm trying to get at.  So, anyway, those factors have to be thought about, avoidable risk, avoidable consequences versus limiting other options.  If I can borrow a term from the statisticians, that being that of losing a degree of freedom, so to speak.
		Another thing I wanted to mention - I'd be remiss if I didn't mention this - I understand that we're looking at the data set, the data presented, but I would like to say something with regards to biocompatability issues.  I know that it's not on the table. I take it that all that's been addressed earlier on, but certainly, when it comes to approving these devices, make sure that we don't overlook issues of bio compatability, bio integrity, and so forth.
		Let's see.  I do want to make one more comment with regards to the secondary endpoint; in particular, the six-minute walk, the O2 max or anaerobic threshold.  I believe that they are somewhat different, but, nonetheless, wanted to say something about FDA Slides 67, 68, which seems to show that the control group is better off than the CorCap along those two attributes.  So, again, that's something that leads me to question in some regards the efficacy of the device.  But once again, going back to what I said earlier, there is also issues of avoidable risk, avoidable consequences, avoiding later on heart transplant.
		I believe that covers it for now. I've taken more than my share of time.  Thank you.
		DR. RAMSEY:  That was excellent, and we appreciate your comments.
		So now we will have Dr. Braier will read the panel recommendation options for pre-market approval applications.  Dr. Braier.
		DR. SACKNER-BERNSTEIN:  Before we do that, could I just raise one more issue, because you're about to lead us into the voting, and I wanted to just bring up one more topic before that.
		DR. RAMSEY:  Okay.
		DR. SACKNER-BERNSTEIN:  Okay.  Thank you.  I think that there's a question that comes to mind based on this trial design that would be important for both the FDA to be considering going forward, as well as any sponsor, in addition to being relevant to this.  What we're testing here, or what is being tested here is a surgical intervention that carries with it a certain amount of morbidity and mortality risk.  It's not really clear exactly how much, but we saw the confidence intervals extended up to a pretty high 30-day mortality.  
		In a case such as this, I personally think that there needs to be careful consideration about whether the index hospitalization is counted, although it may, in many cases, put the intervention at an excessive disadvantage; nonetheless, I think it's important to think about whether it should be counted.  And as we look at the major cardiac procedures here, one could interpret this trial to say that the intervention shifts in time, and shifts the risk of the urgency of a major cardiac procedure because you can schedule the CorCap versus many LVADs, which are done urgently or emergently, as well as transplant, so it may be the advantage isn't, as simply put, as reducing major cardiac procedures that are associated with worsening heart failure, but that it shifts in time when somebody has a procedure.  And as emphasis of this, there's the risk of the procedure itself.  There's also data that's presented in the Acorn clinical study summary that shows that in the MVR group, that if a subject also had a CorCap, that they had a longer length of stay.  Their post op hospitalization was the difference in median, there's no P values or nominal P values here, but it's 9 versus 7 days, post op ICU length of stay is 4 versus 2 days, duration on post op ventilator 12 hours versus 10 hours.  I think there's a certain amount of consistency to the data that says that it would be wrong for us to assume that you never have to count these kinds of index hospitalizations.
		DR. RAMSEY:  Okay.  Thank you.  Good comment, and we'll move it on, back to Dr. Braier.  Go ahead.
		DR. COLLAZO-BRAIER:  The Medical Device amendments to the Federal Food, Drug, and Cosmetic Act, as amended by the Safe Medical Devices Act of 1990, allows the Food and Drug Administration to obtain a recommendation for an expert Advisory Panel on designated medical device pre-market approval applications that are filed with the agency.  		The PMA must stand on its own merits, and your recommendations must be supported by safety and effectiveness data in the application, or by applicable publicly available information.  The definitions of safety, effectiveness, and valid scientific evidence are as follows.  Safety - 21 CFR 860.7(d)1 - "There is reasonable assurance that a device is safe when it can be determined based upon valid scientific evidence that the probable benefits to health from use of the device for its intended uses and conditions of use when accompanied by adequate directions and warnings against unsafe use outweigh any probable risk."
		Effectiveness - 21 CFR 860.7(e)1.  "There is reasonable assurance that a device is effective when it can be determined based upon valid scientific evidence that in a significant portion of the target population the use of the device for its intended uses and conditions of use when accompanied by adequate directions for use and warnings against unsafe use will provide clinically significant results."
		Valid scientific evidence - 21 CFR 860.7(c)2.  "Valid scientific evidence is evidence from well-controlled investigations, partially controlled studies, studies and objective trials without match controls, well-documented case histories conducted by qualified experts, and reports of significant human experience with a marketed device from which it can fairly and responsibly be concluded by qualified experts that there is reasonable assurance of the safety and effectiveness of a device under its conditions of use.  Isolated case reports, random experience, reports lacking sufficient details to permit scientific evaluation, and unsubstantiated opinions are not regarded as valid scientific evidence to show safety and effectiveness."
		Your recommendation options for the vote are as follows.  Approval - if there are no conditions attached.  Number two, approvable with conditions - the panel may recommend that the PMA be found approvable subject to specified conditions, such as physician or patient education, labeling changes, or a further analysis of existing data.  Prior to voting, all of the conditions should be discussed by the panel.  Not approvable - the panel may recommend that the PMA is not approvable if the data do not provide a reasonable assurance that the device is safe, or the data do not provide a reasonable assurance that the device is effective under the conditions of use prescribed, recommended, or suggested in the proposed labeling.  Following the voting, the Chair will ask each panel member to present a brief statement outlining the reasons for his or her vote.
		DR. RAMSEY:  Thank you, Dr. Braier.  At this point, I would ask the voting members of the panel whether anyone has a motion to recommend approval, approval with conditions, or not-approvable.  And I can't go first.
		DR. CRITTENDEN:  I'll make a motion for approved with conditions.
		DR. RAMSEY:  Do I have a second for that motion?
		DR. LASKEY:  Second.
		DR. RAMSEY:  We now have to discuss the condition, so Dr. Crittenden, do you have a condition that you would like to propose?
		DR. CRITTENDEN:  The sponsor should continue with the proposed post hoc analysis, and that we work with the sponsor in terms of narrowing the labeling, because I think the labeling as currently specified is, perhaps, a bit broad.  I would elicit the help of my fellow panel members to help narrow that.
		DR. RAMSEY:  Dr. Laskey.
		DR. LASKEY:  Well, that was not my choice for the condition, so I will not be dragged into this first.  I just had another condition, but I guess we need to deal with the one on the table.
		DR. RAMSEY:  Okay.  So since there's disagreement, we will ask for a second, whether there is a second for that condition.
		DR. SACKNER-BERNSTEIN:  I thought I may have heard two different conditions proposed.
		DR. RAMSEY:  And so for that reason, we have to start with one, Dr. Crittenden's, and whether there's a second for that condition or not.
		DR. SACKNER-BERNSTEIN:  I thought he said two conditions.  One was to urge them to continue with their analysis of the existing data, and the second one being define a more narrowed label.
		DR. CRITTENDEN:  That's correct.
		DR. RAMSEY:  Okay.  Well, then we would want to vote on each of those conditions.  So condition one was to urge continued analysis of the primary cohort.  Is that correct?
		DR. CRITTENDEN:  That's correct.
		DR. RAMSEY:  Do we have a second for that condition?
		DR. LASKEY:  Well, we want to discuss this before we --is that right?  We have a condition on the floor, we should discuss it.
		DR. SACKNER-BERNSTEIN:  I'm just concerned whether "urged" is the appropriate term.  I think there needs to be a little more teeth.
		DR. RAMSEY:  Excuse me.  We do have to have a second first.  We have to have a second to that particular condition, and then discussion.
		DR. SACKNER-BERNSTEIN:  Could I ask Dr. Crittenden to state precisely what he'd like the first condition to be?
		DR. CRITTENDEN:  The first condition ought to be to continue the post hoc analysis that the sponsor provided - agreed to pursue.
		DR. RAMSEY:  That was your first condition.  Is that correct?
		DR. CRITTENDEN:  Yes, that was the first condition.
		DR. RAMSEY:  Okay.  I think I heard something a little different first time.  And when you mean "continue the post hoc analysis", does that mean that -- we might need some more specificity on that.  For example, are we saying that we are approving with only the condition that the post hoc group be part of the PMA, or are we approving the entire cohort, with encouragement that the post hoc group be followed closely?
		DR. CRITTENDEN:  Well, I think I hear what you're saying, so perhaps we ought to go with number two first, and that's narrow the labeling, and then do the post hoc analysis, because I'm not sure following the whole cohort would -- I'm comfortable with that.
		DR. RAMSEY:  Okay.  We have to have a -- I don't think we've had a second.
		DR. CRITTENDEN:  It has not been seconded.
		DR. RAMSEY:  We have not had a second yet, so we have to -- before we have any discussion, we have to have a second on that motion.  And if we have no second, do we come up with a new motion?  Is that correct?  So is there a second to that motion?  Okay.  So there's no second to that motion, so we can go back to have another motion.  And I believe we can go again across all three, approval, approvable with conditions, and not approvable.  Does anybody have a second vote?  If someone wants to specify a condition, a different condition for the approvable with conditions, we can go there, too.
		DR. LASKEY:  Yes, I'd like to put that on the floor.  I would suggest approval with the following condition, which is that we need continued enrollment with more precise estimates of safety.
		DR. RAMSEY:  So that would be continued enrollment in the context of a clinical trial.
		DR. LASKEY:  Correct.
		DR. RAMSEY:  I guess you're saying -- 
		DR. LASKEY:  More.
		DR. RAMSEY:  More follow-up with regard to safety.
		DR. LASKEY:  We need -- I would like to see more assurance that this is a safe procedure in the patient population.
		MS. WALKER:  Could I make a suggestion?
		DR. RAMSEY:  We have to have a second on that, and then have discussion.
		DR. CRITTENDEN:  I'll second that motion.
		DR. RAMSEY:  Now I believe we can have discussion.  Apologies for the -- 
		MS. WALKER:  Perhaps, what the motions are trying to get to is to analyze all existing data that may have been collected under continued access or from other sources, as well as continuing efforts to look at more long-term information that may be available now that was not available previously.
		DR. LASKEY:  No, I'll be blunter.  I want to see those perioperative 30-day rates low.  I want to see the bar graphs get ever-diminishingly smaller than they were at the outset.  I think that we have enough concerns about the efficacy, but I think unless we settle the safety issue in our minds, there shouldn't be a question about whether this is approvable or not, so I think we need more robust estimates of safety, which we have not seen, in my mind, thus far, in this trial.
		DR. CRITTENDEN:  We have the overall data, but at the meeting, the operative mortality was lower.
		DR. RAMSEY:  Can I ask -- let me ask, because this is an important point for clarification.  I think you're -- well, one interpretation of the motion is that the sponsor continue with the PMA to continue to collect data as part of the pre-market application.  That's one interpretation.
		A second interpretation is that they get pre-market approval, but I don't know if I know what the second interpretation is; continue the trial?  The issue is that I think that with a PMA - in some ways you're saying not approvable, because it sounds like you're saying you want more PMA data.
		DR. LASKEY:  Yes.  And this may be beyond the bounds of a regulatory consideration, because if I don't feel the trial is safe, then I should so vote.  But I think I would like to see better estimates of safety than what we currently have.  And that's the condition.
		DR. RAMSEY:  Okay.  So I'm still struggling a little bit with whether to ask for a second for that vote, or to say that we're really saying not approvable.  So, actually, Dr. Sackner-Bernstein, do you want to add something?
		DR. SACKNER-BERNSTEIN:  I think Warren is asking for more controlled trial data, which by definition means that he's saying not approvable.
		DR. RAMSEY:  That's what I am interpreting this as, but I don't want to run afoul of the voting members, so I would need a motion from one of the members for not approvable.  Hold on.  
Okay.  So where we're at, I believe, right now, is we've had a motion, and we would need a second to vote on that.  If we do not have a second on the current motion, which is approvable with conditions, as we've now, I think, clarified.  Right.  The condition of more clinical trial data.  And we just -- I think we may want to -- we can vote for a second on that, or we cannot second it, and we can go to a not approvable.  Well, we can go to a whole different round.  I'm sorry.  So let's start with a second for the current motion by Dr. Laskey.  Again, if there's no motion, we'll go back to the drawing board.  If there is, we'll go to discussion.
		DR. CRITTENDEN:  Ask a point of clarification.
		DR. RAMSEY:  Yes.
		DR. CRITTENDEN:  Dr. Laskey, you want new data, as opposed to them analyzing the data already collected.
		DR. LASKEY:  We want new data, additional data.
		DR. RAMSEY:  So if there's no second, the motion will fail, and we'll go back again.  So is there a second on the current motion?  Okay, so there's no second on the current motion, so now we can go back and entertain -- So I'm going to turn to Dr. Braier to make sure I say this right.  My understanding is that we have to ask for more conditions on the current motion.  
		DR. SACKNER-BERNSTEIN:  I don't think approval with conditions was ever -- was that seconded?  It was.  Okay.  
		DR. RAMSEY:  That's what we're discussing here.  So my understanding is that -- I believe Dr.  Crittenden seconded it.  So, again, help me here.  We are asking are there any more conditions.  Okay.  So unless we don't have other conditions, then we will vote on the current motion.
		PARTICIPANT:  Excuse me.  Could she read the types of conditions again?
		DR. RAMSEY:  Well, this is the problem.  We don't really have a condition here, so I'm trying to argue to just start over again, but I've been told I have to follow procedures, so we have to sort of vote on this particular rather unclear approvable with conditions.  So could I have a vote for all in favor of the current approvable with conditions motion?  Okay.  And now all opposed to the current approvable with conditions motion?  No, we just vote on this one, and then when we get to the final, then we will have comments.
		Dr. Crittenden, are you abstaining?
		DR. CRITTENDEN:  I'm sorry.  I voted in the affirmative.  I want to -- I voted for the condition, but I've been outvoted by three other members of the panel.
		DR. RAMSEY:  Okay.  So it is -- I'm sorry, I didn't see it.  So we are 3-1 against.
		DR. CRITTENDEN:  3-1, correct.
		DR. RAMSEY:  And now we will go back to a new motion for a recommendation.  Again, the options are approval, approvable with conditions, and if you have that, we need to have a description of the condition, or not approvable.  Do I have a motion for one of those three?
		DR. SACKNER-BERNSTEIN:  I think what's already been said, in essence, is that there should be a motion for non-approvable.
		DR. RAMSEY:  Do I have a second for that?
		DR. LASKEY:  Second.
		DR. RAMSEY:  So we are now -- do we have any discussion on the motion?
		DR. HUGHES:  Are we allowed to discuss, too, over here - the two of us?
		DR. RAMSEY:  Okay.  So yes, you are allowed.  Dr. Hughes, would you like to go first?
		DR. HUGHES:  Okay.  First off, I think it would be harsh to go with not approvable, but as I understand the way it's presented, you really can't use post market surveillance as a substitute for a pre-market kind of condition.  What's on my mind is that the prospective study - the post - what is it - post market study does need to be done.  That's the way I see it, as opposed to - I'm sorry - prospective study, prospective study needs to be done, as opposed to a prospective analysis of existing data.  And I believe it might be possible to make the prospective study a part of post - what is it - post market surveillance.  I think you can do that logically, but I don't believe you can do that regulatorily.  I don't think so, so I'm just making a little comment, that I think that non-approvable is harsh, but I don't see a way out of it, if there has to be additional studies, additional data that has to be gathered.
		DR. RAMSEY:  Ms. Walker, do you have a comment?
		MS. WALKER:  Yes.  I think that there is data that we have not been privileged enough to see at this point.  And before requiring an entirely new study and saying a non-approvable, I think that that data deserves to be reviewed and analyzed by the agency, as well.  I mean, earlier we had a mention of data that obviously they had not seen, so prior to the time that the company is pressed into another either a separate or expansion of a clinical trial, we'd like that data to be analyzed, as we know that they have continued to collect data both in the continued access protocol, and in the long-term follow-up of the 300 patients that were entered into this study.
		DR. RAMSEY:  Right.  This panel is making a recommendation to the FDA, which they can act on, or not act on.  Do you have any other discussion on the motion for not approvable?
		DR. SACKNER-BERNSTEIN:  I think the statement that you made, Allen, about the non-approvable being harsh is something that I would agree with.  The problem that we're faced with is, based on the regulations, there's just so much uncertainty.  And I think that Warren put it correctly when he was talking about the safety of the procedure.  I think there's a safety long-term where the confidence intervals are very wide, much wider than was prospectively defined as an acceptable safety parameter in the study protocol.  And so with uncertainty about safety, I think right there we're in trouble, so that you add that uncertainty about safety with uncertainty about benefit because of many of the methodologic issues that have come up, and it becomes very, very difficult to provide an estimate of risk benefit ratio.  I mean, every therapy has a risk, so that benefit is always weighed against the risk.  But with such uncertainty in both the numerator and the denominator, I believe that there just can't be a way to look at this data as it exists, even if there were long-term follow-up that were available from this cohort and the open label continued access program that would be enough to tell me that there's reasonable assurance of safety, that there's reasonable assurance that the probable benefits outweigh the risk.  I just don't think we have enough information to be able to make that statement.
		DR. RAMSEY:  Do we have any more discussion?
		DR. LASKEY:  I think the rest is really editorializing.  This has been agonizing, or something shy of agonizing.  We are extremely sympathetic to the investigators.  We are clinicians ourselves.  There is a need for this.  There's no question, and we're bending over backwards to try and find a reason to help patients who fall into this particular niche, but we can't find it.  And then, above all, in my mind is the safety signal.  It's just too hard to look away from.  Forget about the efficacy, forget about imputation, forget about how off we are in classification - if it's not safe, we can't go any further.
		DR. CRITTENDEN:  But, Warren, these patients are already on the risk highway.  I mean, it's not that they're going to face zero risk if they have nothing done.
		DR. LASKEY:  Hence our - to use Clyde Yancy's word - angst.  There's no question we walk this with this line, but we don't want to hurt them in the process of getting them to the part of the curve where there's benefit.  And I've yet to see that part of the curve where you have to get past your up front mortality, if they live passed this procedure, to derive benefit.
		DR. CRITTENDEN:  I suspect this is part of a specialty-specific type of risk aversion. I think if you look at the panel vote - not that that's germane now - but I think most of the surgeons voted for it then.  I think you need to kind of live with these things to really kind of have a comfort level with this.  I guess part of being an interventionist is Bard Parker versus a catheter, but I think that we're denying patients something that is of benefit, and I think it's going to be very difficult to define this, otherwise.
		DR. RAMSEY:  Is there any more discussion?
		DR. LASKEY:  I know this isn't meant to be a showdown, but what's the benefit?  Have we been clear about that?
		DR. CRITTENDEN:  I think there's a symptomatic benefit, and there's an avoidance of secondary procedures.
		DR. RAMSEY:  Any more discussion?  Okay.  At this point, I would like the voting members to vote.  The motion is for - which has been seconded - is for not approvable.  All in favor of that motion raise your hand, please.  All opposed?  And there are no abstainers, so the motion for not approvable will pass.
		At this point, we have - we want to ask each panel member to state a reason for his or her vote, and I'll start on the right with Dr. Laskey.
		DR. LASKEY:  I think I've said enough.  It's really extremely difficult, extremely soul searching to have to make this call at this point, we're so late in the game, but we have to -- we've been instructed to deal with the data that we have at hand.  And this is not about a Bard Parker versus catheter.  We all face patients at high risk every day, and we just try not to rub them out in the process of doing better, so that's the reason for my vote for disapproval. I just didn't see the safety signal that would allow us to look passed some of the ambiguity, to be euphemistic about the efficacy.
		DR. RAMSEY:  Thank you, Dr. Laskey.  Dr. Sackner-Bernstein.
		DR. SACKNER-BERNSTEIN:  A similar perspective.  When the potential risk in terms of mortality risk looked at either in the 30-day time frame as perioperative, or over the course of the study up to the common closing date, cannot exclude such a large increased risk, there has to be a really compelling, irrefutable, internally consistent, and without doubt clinically meaningful benefit.  And I think that the safety signal just raises the bar so high that when you look at the efficacy data, that whether the argument falls on one side or the other of the imputation methodology, or the core lab methodology, et cetera, there's just not enough there to outweigh that concern about safety.
		DR. RAMSEY:  Thank you.  Dr. DeMets.
		DR. DeMETS:  I expressed earlier some of my reservations or concerns about the primary outcome.  I mean, this is a single trial, a small trial where there's been discussion about the primary outcome.  While there is some supportive evidence in the secondary outcomes, the ones that you hope for as impressive as you would like to see.  So because of those reasons, I guess I'm not overwhelmingly convinced.
		DR. RAMSEY:  Thank you.  Dr. Crittenden.
		DR. CRITTENDEN:  I voted against the motion because I think the sponsors have shown that there is some efficacy to this, though I'm admittedly on the fence about the core lab versus site New York Heart Association Class specification, and multiple imputation, but I think there is sufficient evidence that you reduce the need for LVAD placement and cardiac transplants.  And I think in the hands of the surgeons who will be doing this, that this is a safe procedure, certainly for patients who have very little alternative, other than continued medical therapy.
		DR. RAMSEY:  Thank you, Dr. Crittenden.  So the panel has voted in favor of a recommendation for not approvable.  At this point, Dr. Weinstein, do you have any further comments?
		MR. WEINSTEIN:  Yes.  I would just like to say thank you to all the panel members who contributed so well to the discussion here today, and especially to Dr. Ramsey, our Chair, for your sense of fairness, and balance.  And if you ever want to make a career change, I think that you would make a wonderful Ombudsman.  
	(Laughter.)
		MR. WEINSTEIN:  I'd also like to thank Acorn for all the hard work that went into your presentations and your case today, as well as FDA for all the hard work that you did in preparing for this meeting.  I'd like to thank Dr. Braier, the new Executive Secretary for the Dispute Resolution Panel.  And I'd like to thank Office of Management Operations for all the logistical support, especially Ann Marie Williams, and Shirley Meeks.  And, apparently, we're not finished yet.
		DR. RAMSEY:  I think Les is going to take back his recommendation for me to work with the FDA.  I neglected to note, and I am sorry to drag this out for all involved, that since we have voted not approvable, the panel must now identify what they believe is needed to make the PMA approvable.  Now I presume this is only for the people who voted against, or as not approvable, that Dr. Crittenden doesn't have to because he feels that it is sufficient.  Is that correct?  Even Dr. Crittenden?  He can certainly have a comment.  Okay.  So, again, I apologize for not picking that up first; but, Dr. Laskey, do you have a specific recommendation to make the PMA approvable?
		DR. LASKEY:  I really need to think about this.  I don't think there's any way to salvage the current - what we're looking at on the table right now.  That's what we were voting on, is my understanding.  We're searching for ways to make this treatment modality safe and effective, and I guess short of an additional trial, which perhaps can be creatively configured using either an adapted design, or Bayesian design, or some very creative way to look at boundaries and safety endpoints, that, I guess, is my only suggestion.  But what we have here, is what we have here.
		DR. RAMSEY:  Thank you.  Dr. Sackner-Bernstein.  And I just want to make a comment that this is a very hard thing to ask the panel to do.  I'm not sure I agree with asking the panel to do this sort of on the fly, but I am required to ask you to identify if you need to do anything to make the PMA approvable.
		DR. SACKNER-BERNSTEIN:  I would agree that it is a difficult question to answer, and probably would require weeks and months of planning, and considering different options.
		But studies should be designed in a way that the upper confidence interval of safety becomes some number that's a more acceptable range, perhaps where the initial protocol pegged it at 15 percent, maybe a little more, maybe a little less, but I think that where it is is too high.  And in the setting of one where the confidence interval were to that level above one, the upper confidence interval, then there needed to be convincing evidence that there was a clinically meaningful benefit that was realized.
		DR. RAMSEY:  Thank you. Dr. DeMets.
		DR. DeMETS:  Well, I think this data that at least we've had so far has been analyzed and interrogated pretty thoroughly, so I don't see that that is going to help.  I guess I'm a victim of my past, but in other heart failure trials where we've had this conundrum, in most of those cases, a second trial was done to try and resolve the issue, and so I know devices aren't drugs, and I know the laws are different, but I can't help myself.  I still think about it the same way, so I think that short of another study, where the issues of bias are - I mean, it will never be perfect, as already alluded to, but I think they should be thought about, and probably larger.
		DR. RAMSEY:  Thank you.  Dr. Crittenden, you are welcome to add a comment, if you would like.
		DR. CRITTENDEN:  I don't have any further comments.  Thank you.  
		DR. RAMSEY:  Do the non-voting members have any comments at this point?  Okay.  With that, and Mr. Weinstein's nice thank-yous, I will add my thank you to the entire group.  I have tried my best to make sure that everyone has a chance to hear the evidence, and that it was a balanced presentation.  And if either party feels that that was not the case, I definitely want to hear about it.  But, otherwise, this meeting is adjourned.
		(Whereupon, the proceedings went off the record at 4:47 p.m.)