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Ann Thorac Surg 1999;67:723-730
© 1999 The Society of Thoracic Surgeons

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Original Articles

The REMATCH trial: rationale, design, and end points

^a International Center for Health Outcomes and Innovation Research, Columbia University, New York Presbyterian Hospital, New York, New York, USA
^b Department of Surgery, College of Physicians and Surgeons, Columbia University, New York Presbyterian Hospital, New York, New York, USA
^c Department of Medicine, College of Physicians and Surgeons, Columbia University, New York Presbyterian Hospital, New York, New York, USA
^d Department of Psychiatry, College of Physicians and Surgeons, Columbia University, New York Presbyterian Hospital, New York, New York, USA
^e Department of Neurology, College of Physicians and Surgeons, Columbia University, New York Presbyterian Hospital, New York, New York, USA
^f Division of Biostatistics, School of Public Health, Columbia University, New York, New York, USA
^g Brigham and Women’s Hospital, Boston, Massachusetts, USA
^h National Heart, Lung, and Blood Institute, Bethesda, MD, USA

Accepted for publication November 10, 1998.

Address reprint requests to Dr Gelijns, International Center for Health Outcomes and Innovation Research, Columbia University, Harkness Pavilion, Room 758, 180 Fort Washington Ave, New York, NY 10032
e-mail: acp10{at}columbia.edu

	Abstract

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 
Background. Because left ventricular assist devices have recently been approved by the Food and Drug Administration to support the circulation of patients with end-stage heart failure awaiting cardiac transplantation, these devices are increasingly being considered as a potential alternative to biologic cardiac replacement. The Randomized Evaluation of Mechanical Assistance for the Treatment of Congestive Heart Failure (REMATCH) trial is a multicenter study supported by the National Heart, Lung, and Blood Institute to compare long-term implantation of left ventricular assist devices with optimal medical management for patients with end-stage heart failure who require, but do not qualify to receive cardiac transplantation.

Methods. We discuss the rationale for conducting REMATCH, the obstacles to designing this and other randomized surgical trials, the lessons learned in conducting the multicenter pilot study, and the features of the REMATCH study design (objectives, target population, treatments, end points, analysis, and trial organization).

Conclusions. We consider what will be learned from REMATCH, expectations for expanding the use of left ventricular assist devices, and future directions for assessing clinical procedures.

	Introduction

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 
Population-based studies estimate that heart failure afflicts between 3 million and 4 million Americans, with about 400,000 new cases being diagnosed each year [1, 2]. Although there are a number of investigative therapeutic modalities for treating end-stage heart failure, the two primary treatment options available are pharmacologic therapy and cardiac transplantation. Advances in medical therapy have had an important impact on symptom status and short-term survival of patients with moderate to severe heart failure. However, existing pharmacologic agents have met with only moderate success in patients with class IV heart failure, and the 1-year survival rate is only 40% to 50% [3]. For these patients, cardiac transplantation, with 5-year survival rates of around 65%, is the more desirable treatment option [4]. Yet the success of cardiac transplantation remains limited by the complications of long-term immunosuppression, the development of allograft coronary artery disease, and, most importantly, the current serious shortage of donor organs.

Since the inception of the artificial heart program at the National Institutes of Health in 1964, a variety of circulatory support devices have been developed for the temporary support of patients with end-stage heart failure. In September 1994, the Food and Drug Administration (FDA) approved the pneumatically driven left ventricular assist device (LVAD) from Thermo Cardiosystems Inc (TCI) for bridging such patients to cardiac transplantation. The vented electric (VE) version of this device is fully "wearable," thus eliminating the restrictions imposed by the tether to the pneumatic console, and FDA approval was recently obtained. Simultaneously, the FDA approved an electric LVAD from Baxter CVG, Novacor Division. The bridge-to-transplantation experience has demonstrated the ability of LVADs to support the failing circulation of patients with end-stage heart disease [5–7]. Indeed, short-term LVAD support in this select population of patients can normalize hemodynamics, reverse end-organ dysfunction, improve exercise tolerance, allow discharge home, and provide reasonable quality of life with an acceptable incidence of major adverse events [8–11].

The clinical promise of LVADs and the limitations of existing treatment options for patients in advanced heart failure (ie, the shortcomings of medical therapy and the severe shortage of donor organs) can be expected to encourage transplant centers to begin using the VE device not only as a bridge, but also as an alternative to transplantation [12]. This broadening of use raises several critical issues: What effect on survival will this device have compared with alternative treatment strategies? What is the "life expectancy" of the device, and what is its safety profile? Will the short-term improvements in quality of life offered by this device translate into an acceptable life-style? Will the up-front costs of implantation be offset by the long-term benefits?

Current standards of evaluation of the effectiveness of the LVAD as a long-term therapy for end-stage heart failure necessitate a randomized clinical trial. The selection of the appropriate comparative treatment will depend on the target population. The Institute of Medicine has estimated that about 60,000 individuals between the ages of 15 and 85 years could benefit from mechanical cardiac assistance [13]. Today and, in all likelihood, for years to come, patients older than 65 years are excluded from cardiac transplantation. In view of the fact that the majority of the potential recipients of mechanical assistance are more than 65 years old, we are initiating a randomized, prospective trial to compare the "wearable" LVAD with optimal medical treatment for patients in end-stage heart failure, who are ineligible for cardiac transplantation. The device selected is the TCI HeartMate VE LVAD.

We review here our approach to designing the Randomized Evaluation of Mechanical Assistance for the Treatment of Congestive Heart Failure (REMATCH) trial. Comparing surgical with medical therapies in a clinical trial brings up a number of methodological and ethical issues. We raise these issues and then discuss how we dealt with them in REMATCH.

	Randomized clinical trials in surgery

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 
In today’s rapidly changing health-care environment, there are increasing demands for more rigorous evidence of the benefits, risks, and costs of new clinical interventions. This is particularly true for surgical interventions that are highly visible and consume a large amount of resources, such as the LVAD [14]. The trend toward more strict evaluation has been reinforced by the fact that new surgical interventions often involve medical devices whose acceptance into clinical practice requires FDA approval. In recent years, the device branch of the FDA has been moving toward the adoption of randomized, controlled clinical trials. The techniques used to design and conduct surgical trials, however, are relatively new in comparison to the well-developed schemes used to test new pharmacologic treatments. Thus, surgical trialists must contend with unique technical (surgical), ethical, and methodological issues [15].

One of the interesting complexities associated with multicenter surgical trials is that the skill of the surgeons can vary considerably, and this can dramatically affect the outcome of the trial. The results of a comparative surgical trial in which there is selective assignment of the surgeon or clinical center to a particular procedure may have more to do with differences in the expertise of the surgeons and clinical centers than with the inherent differences of the two surgical approaches. This is often the case with an emerging surgical device such as the LVAD. Similarly, the skill of the surgeon and the clinical center involved in a clinical trial will also affect the generalizability of the results. Routine clinical practice often may not yield the same outcomes achieved by the most skilled surgeons at tertiary-care institutions. To make results more generalizable, trials now include a variety of venues of care, both university based and community based.

Another feature of surgical trials not typically found in pharmaceutical trials is that surgical procedures often undergo extensive refinement, and the achievements of the later phases of development usually far surpass those of the early experimental operations. Consequently, the results of a comparative clinical trial of a new surgical intervention will depend on when the comparison was made. This poses a dilemma for selecting the optimal time to bring a surgical procedure to trial: Waiting too long may result in widespread use of the procedure and loss of the opportunity to perform a trial, whereas starting too early may result in evaluating a procedure that is not yet fully developed and therefore may not reflect the procedure that will ultimately be used [16].

There are also ethical concerns in the random assignment of patients in surgical trials. Regardless of the modality of care, interventions that offer potential breakthroughs in the treatment of life-threatening illnesses present hardships for both the patient and the investigator in accepting the randomization process. In contrast to double-blind pharmaceutical trials, both the investigator and the patient in surgical trials will immediately know the treatment assignment and will have expectations regarding outcome. This will deter some patients and physicians from ever entering into such a trial. Others will choose to participate, but on assignment to the control arm, will seek treatment outside the protocol, leading to a loss-to-follow-up or out-of-protocol crossover, potential death knells for clinical trials. Another ethical dilemma arises when the immediate treatment effect and its associated quality of life are radically different between treatment groups. A case in point is the comparison of amputation and limb-sparing therapy for osteogenic sarcoma of an extremity [17].

Blinding, an important technique for controlling observational bias, is an issue in surgical trials. It is impossible for the treating surgeon to be blinded. A partial solution is to have outcome events judged by independent, blinded observers who did not treat the patients. However, solutions that will control for the potential bias imposed when patients are unblinded in surgical trials are not optimal. Clearly, if the two interventions being compared are surgical procedures, it may be possible to keep the patient unaware of which procedure was administered. However, patient blinding is not possible if one of the comparative therapies is nonsurgical.

The measurement of survival in trials that compare surgical and medical therapies poses methodological challenges [18]. In particular, if surgical therapy involves a high up-front operative risk but subsequently offers a reduced mortality compared with the medical arm, the survival curves are likely to cross. Analyzing the differences between such curves is highly dependent on the analytical method chosen and the time frame of the analysis. Most analytical methods (eg, log-rank and Wilcoxon) average risk over the follow-up period. Extending or reducing the follow-up time has the potential to reverse the ordering of estimated relative efficacy because less or more weight, respectively, will be given to the mortality in the perioperative period. Moreover, when survival curves cross, it means that there is no consistent proportional relationship in the relative mortality of the two treatments. Such a finding would violate a basic assumption that is implicit in using proportional hazard methods, the mainstay of survival analysis procedures.

Ultimately, the choice of which treatment is better goes beyond determining whether the curves differ in a significant manner. The choice must address the relevant question of whether the up-front operative mortality risk is adequately offset by the improvements in quality of life as well as subsequent risk of mortality. Establishing such criteria for the study’s target group involves the opinions of those conducting the trial and thus must be specified before study initiation. Although these opinions are relevant for analyzing the outcomes of the two treatment groups, making clinical decisions for an individual patient requires taking into account the patient’s preferences and attitude toward risk.

	REMATCH trial phases and objectives

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 
Having reviewed the challenges of conducting surgical clinical trials, we now turn to how we dealt with them in designing REMATCH. Our research has been divided into two phases: a multicenter randomized pilot study of limited power to detect survival differences and a more definitive multicenter randomized controlled trial.

Phase I: the pilot study
The pilot study had three objectives. The first was to obtain the essential data on patient and device survival needed to plan a large-scale clinical trial. Although there was considerable experience using this device to support transplantation candidates, the LVAD had never been implanted in the older and sicker population of patients, who are ineligible for transplantation. Second, the VE device was still undergoing major modification; for instance, the driveline was recently reengineered. The pilot study served to further the experience of the surgeons with the modified device. Third, the FDA mandated a randomized pilot study to determine whether the randomization process was feasible in a surgical trial of a life-threatening condition.

The pilot study, still ongoing, has randomized 21 patients. Despite the potential pitfalls mentioned earlier, randomization went smoothly. A successful aspect of this trial is that it provided the essential patient and device reliability data necessary to plan the second phase of the study. It also gave the surgeons experience with the newly designed device. Moreover, it suggested that implanting the device in an older and sicker population did not adversely affect perioperative mortality.

An important design issue in the pilot study was whether the device was to be compared with standard community heart failure care or optimal medical management. The former, as already suggested, would give results that were more generalizable, whereas the latter would provide a more stringent test for the device. It was the consensus of the investigators that the extraordinary nature of the risks and life-style implications of living with an LVAD merited a more rigorous test and that therefore a comparison with optimal medical management would be more appropriate. Moreover, because surgical experience with these devices has been limited to a highly specialized group of cardiac surgeons, medical therapy should also be administered by comparable experts in heart failure therapy. Because there are no explicit guidelines for optimal medical management of patients with end-stage heart failure, part of the pilot mission was to develop standards for both the medical treatment and the surgical treatment of these patients.

As previously noted, survival analysis for controlled surgical trials often must deal with crossing survival curves, and early LVAD data supported this notion for the REMATCH trial. To address this, our initial approach was not to compare entire survival curves (eg, using log-rank testing), but rather to measure relative benefits at a point when a consistent difference between treatment strategies could be discerned. Thus, our null hypothesis was that the LVAD conferred no benefit at the 2-year end point, not that survival functions were equivalent. Our alternative hypothesis was that the LVAD conferred a clinically important benefit at 2 years (33% reduction in mortality), despite crossing hazards and survival functions, not that the treatments had proportional hazards. Because 2-year survival is essentially binary, the analytical test chosen for primary analysis was the Fisher exact test. The disadvantage of this type of analysis is that it turns a blind eye toward survival benefits that might appear before or after the 2-year mark. It avoids, however, the risk of drawing a conclusion based on a transient advantage in the medical therapy arm. Since we formulated this initial analytical plan, experience with LVAD implantation and management has evolved, and perioperative mortality rates have fallen, both for the patients in the pilot study and "bridged" patients in general. Our concerns about late crossing survival curves have paralleled this trend, and we therefore revised our analytical plan for phase II (REMATCH) accordingly.

Phase II: the randomized controlled trial
Objectives
The overall purpose of the REMATCH trial is to evaluate the efficacy, safety, and cost-effectiveness of "wearable" LVADs versus optimal medical therapy in the treatment of end-stage heart failure. The primary objective of the trial is to determine the effect of the LVAD on mortality from all causes. The trial has a broad range of secondary objectives, including analyzing cardiovascular-related mortality and worsening of heart failure, as measured by the use of hospitalization. Other secondary objectives include the assessment of functional status, health-related quality of life, and preferences of patients for the outcomes they experience, which then can be used to calculate their quality-adjusted survival. Contrary to the past, when economic analyses were often afterthoughts, a cost-effectiveness analysis has been explicitly incorporated in the design of this trial. Because the trial results will be submitted to the FDA for approval of the VE LVAD for this indication, safety is an important end point. This trial will compare the incidence of adverse events, including infections, thromboembolism, end-organ dysfunction, arrhythmias, and myocardial infarction, in both groups as well as document the incidence of device-related morbidity, including malfunctions, thrombosis, bleeding, and development of right heart failure (requiring a right ventricular assist device or inotropic therapy) in LVAD recipients.

Characterization of patient population
The trial targets patients with New York Heart Association class IV heart failure who are older than 18 years and are not pregnant. To qualify for REMATCH, patients must be ineligible for cardiac transplantation for one or more of the following reasons: age greater than 65 years; presence of insulin-dependent diabetes mellitus with end-organ damage; chronic renal failure with documentation of a sustained serum creatinine level higher than 2.5 mg/dL for longer than 90 days before randomization; and any major comorbidity (physical or psychiatric) that would make the patient ineligible for cardiac transplantation. Thus, we anticipate that most of the patients in the trial will be older and have comorbid diseases that would preclude transplantation.

This raises the two questions of whether patients will be too high an operative risk and whether their survival will be long enough, given the presence of other mortality risks, to reap the "long-term" benefits of device implantation. As noted, we found in the pilot study that the complication rates of LVAD insertion in the target population appear to be similar to those in patients younger than 60 years who are enrolled in the "bridge" trials. Although the pilot study was not long enough to address the longer-term survival question, other evidence suggests that the 3-year survival in the target population will not be substantially less than that for a transplantation-eligible population. In particular, the increment in age-specific annual mortality rates for patients aged 65 to 70 years compared with patients 55 to 60 years old is only 2%. Further, the excess annual mortality rates for comorbidities such as insulin-dependent diabetes mellitus is about 4% annually. The added effect of age and comorbidity should not have a substantial impact on survival during the period of study.

In addition, patients must fit the following cardiac profile: They must have experienced New York Heart Association class IV heart failure for at least 90 of the last 120 days before randomization. They must have a maximal oxygen consumption of 12 mL · kg^-1 · min^-1 or less with attainment of anaerobic threshold or have been resistant to weaning from intravenous inotropic therapy within 14 days before randomization. Attempts at weaning must be met with hemodynamic compromise, such as hypotension, reduction in renal function, or worsening of heart failure symptoms. Patients must be on a regimen of digoxin, diuretics, and an angiotensin-converting enzyme inhibitor (unless intolerant) for at least 90 of the 120 days before randomization. The patient can be receiving ß-blocker or angiotensin II antagonist therapy provided it has been in use for at least 90 of the 120 days before randomization. Within this period and despite active pharmacologic treatment, left ventricular ejection fraction must be 0.25 or lower. The patient cannot be enrolled in a clinical trial in which mortality is an end point, cannot have received any investigational agent within 30 days of randomization, and must not have undergone a cardiomyoplasty or ventricular reduction operation. Both these procedures have the potential to alter the physiology of the heart failure, and this could induce a response to treatment that would be uncharacteristic of dilated cardiomyopathy and have an unknown effect on survival. Moreover, these procedures impose a technical challenge for LVAD implantation. The exclusion criteria for the trial are provided in Appendix 1.

Characterization of treatments
Patients randomized to the assist device will receive the TCI HeartMate VE LVAD and optimal medical management. The device will be implanted in either the preperitoneal pocket or intraperitoneal cavity, depending on the surgeon’s preference. Aspects of the surgical management that will be standardized for all centers include preoperative measures (such as antimicrobial prophylaxis, preoperative scrub and shave, and operating room precautions), intraoperative measures (such as driveline placement, antibiotic irrigation, and pocket drains), and postoperative measures (eg, systemic antimicrobial agents, exit-site dressing changes, and driveline immobilization).

Patients randomized to the optimal medical management only treatment group will be treated with digoxin, diuretics, and an angiotensin-converting enzyme inhibitor. If angiotensin-converting enzyme inhibitors cannot be tolerated because of allergy or hypotension, then angiotensin II antagonists should be considered. Patients can receive treatment with a ß-blocker at the investigator’s discretion. The goals of therapy are twofold: to ensure that systemic perfusion maintains organ function sufficiently to meet the resting metabolic needs necessary for survival and to reduce ventricular filling pressures sufficiently to achieve and maintain relief from symptomatic resting congestion. Stabilization in some patients may require short-term intravenous pharmacologic support or mechanical fluid removal, which can subsequently be discontinued in favor of other therapies.

Design and end point analysis
The trial will be a parallel group study with random assignment of eligible patients to treatment with the VE LVAD or optimal medical management in a 1:1 ratio. The randomization will be stratified by center and blocked to ensure approximately equal numbers of patients in each arm of the trial throughout its course, thereby facilitating efficient interim analyses [19]. The primary analysis will be by intention-to-treat, including all patients in their randomization arm regardless of whether they received the randomization treatment.

The primary analysis will compare survival rates in the LVAD and medical arms. We will compare survival distributions using the log-rank test and subsequently adjust for differences in baseline predictors of outcome (eg, degree of heart failure, age, comorbidities, and clinical center) using the Cox proportional hazards model. To account for the possibility of finding nonproportional hazards, we will also conduct restricted mean life modeling [20], which does not require proportional hazards, and Cox modeling with time-by-treatment interactions.

A review of the literature suggests that the 2-year mortality rate for patients receiving medical management is approximately 75%, and we hypothesize that use of the LVAD will reduce this rate by a third to 50% or more (our baseline assumption) [3, 21]. Because there is the potential for the device to increase mortality, all statistical tests will be two-tailed. It is possible that the baseline mortality estimates in medically managed patients have been overestimated; a more cautious estimate of the 2-year mortality rates may be as low as 60% and 40%, respectively. Should we observe these latter rates in RMATCH and should survival follow an exponential pattern, the hazard ratio for LVAD to medical management would be 0.56. To detect a difference of this magnitude with 80% power in a log-rank test, we would need to accumulate a total of 92 events (ie, deaths) in the study as a whole [22]. If the more extreme mortality rates hold (75% with medical management and 50% with the LVAD), the hazard ratio would be 0.5, and 92 deaths would give a power of 91%.

We expect to randomize patients at a rate of 7 per month. If randomization is continued for 20 months, under the assumptions of uniform accrual and exponential survival, we will reach 92 deaths by about 38 months after the beginning of randomization (under our baseline mortality assumption). If the more conservative mortality assumption holds, the mortality event target (92) would be achieved by 48 months. In any event, we will continue survival follow-up until we reach 92 deaths.

Patient crossover from medical therapy either to LVAD therapy or cardiac transplantation would reduce the power of the study and, if extensive, compromise the validity of the intention-to-treat analysis. For a variety of reasons, we believe that crossover will be very limited. First, we require surgical implantation within 24 hours of randomization, thus minimizing the chance that the patient assigned to surgical therapy would not receive it. Second, in the United States, the device is not available for off-protocol use in nonbridge patients. Our patient population is, by definition, ineligible for cardiac transplantation, so there will be no crossover to transplantation unless some centers radically change their policies (and more hearts become available). This development is highly unlikely given that the availability of donor hearts has not changed in the last 5 years and that the pool of truly eligible recipients has grown substantially.

The study will investigate several secondary end points that will be critical in determining the practicality of implanting LVADs as a long-term treatment. Health-related quality of life, which is a complex concept that requires multiple dimensions to capture, is an essential measure for characterizing the relative experience of LVAD patients. Two instruments have been chosen for this purpose: the Minnesota Living with Heart Failure questionnaire, a disease-specific measure, and the Short Form 36 Health Survey, a generalized health profile [24, 25]. Primary importance will be assigned to two dimensions: physical functioning and emotional well-being. Objective measures of physical functioning will be captured by the physician-rated New York Heart Association classification, the 6-minute walk test, and maximal oxygen consumption determinations [23].

In addition to measuring quality-of-life using the above health profiles, the EuroQoL will be used to assess preferences or uses for the various states of health experienced by patients in the study [26]. This instrument generates a numerical score on a uniform scale (from 0 to 100) reflecting the values held for the quality of life experienced. These scores will be used as quality adjustment factors in the calculation of quality-adjusted life years, which, in turn, will be applied in the calculation of incremental cost-effectiveness.

The cost or numerator in the cost-effectiveness ratio will be based on data collected directly during the trial. These data will include direct medical care costs (eg, diagnostic tests, medical therapy, and surgical treatment), nonmedical care costs related to treatment (eg, travel to hospital and clinic), the monetary value of time spent by unpaid caregivers (eg, family and friends), and the value of the patient’s time spent in treatment. Given that most patients will be Medicare recipients, health resource use will be derived primarily from the Medicare health care claims database. These services and products will be valued by the ratio-of-cost-to-charges method for each providing hospital. Physician services will be valued by Medicare payments and drugs, by applying average prices from national average wholesale price data. In addition, patients will be asked to keep a diary of nonreimbursed expenses and time donated by others for their care.

Organization and conduct of trial
This trial involves both public and private institutions. The REMATCH study is supported through a cooperative agreement with the National Heart, Lung, and Blood Institute. In addition, TCI will provide financial support and LVADs for the trial. Because TCI has a financial interest in the results of the trial, the company will not be involved in the data collection process or in the analysis of end points. The FDA approved an investigational device exemption in April 1996 for the manufacturer, TCI. Patient care costs, except for the initial LVAD implantation admission, will be supported by the Health Care Financing Administration, which will also provide access to its data files for purposes of cost-effectiveness evaluation.

The study will be conducted at multiple sites throughout the United States (Appendix 2). These centers include both academic medical centers and community-based hospitals with the expertise to provide sophisticated treatment of advanced heart failure. The Data and Clinical Coordinating Center is located at Columbia University, New York. Randomization will be done centrally at this center, and patient enrollment will be overseen by a clinical "gatekeeper." The trial will employ a newly developed remote data-entry system. Coordinators at the clinical centers will complete case report forms on laptop microcomputers, and data will be transmitted automatically each night, in electronic form, by modem to the Data and Clinical Coordinating Center. The program has features to simplify the form-completion process, such as automatic fill-in of key variables and pop-up menus for structured text variables (eg, medications). The program automatically performs range and logic checks.

To ensure consistency in the expertise of both the surgical and medical investigators in this trial, we have established guidelines for surgical and medical management as well as explicit criteria for the approval of investigators. Given that the primary end point is survival, observational bias should have little effect. Nonetheless, cause of death will be adjudicated by an independent committee. Important secondary end points, such as quality of life, will be elicited from the patient directly, thereby minimizing bias imposed by the treating physician.

We began enrollment in May 1998 and anticipate completing enrollment in 18 months. Failure to meet enrollment targets will lead to the addition of new clinical centers and, if necessary, to the extension of the trial.

	What will we learn from REMATCH?

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 
Currently, there is a lack of information about the long-term effects of LVADs on survival, quality of life, and costs, and this trial is designed to address these gaps. In addition, this trial will provide important information on device reliability and on the long-term safety profile of the device. Such findings will be critical for determining the exact role of LVADs among the treatment options available for patients with advanced congestive heart failure. By postulating that the LVAD will decrease mortality by at least 33%, we have set a hard test for the device. However, as mentioned, in view of the important implications of LVAD implantation for both the patient and the society at large, we believe that this test is an appropriately rigorous and clinically relevant "benchmark" for acceptance.

Observations made during REMATCH will serve as the basis for FDA approval of this device and will likely support decisions for its adoption into practice by the broader medical community. Whether the expectations for performance established during REMATCH are achievable in more wide-scale usage will be an important question to address and may need to be looked at continually. This was certainly the case for another high-profile procedure, coronary artery bypass grafting, and its indications for use and the technical aspects of its performance have evolved considerably since early trials, as did its cost. In fact, much of what we now know about the long-term effectiveness of coronary artery bypass grafting as well as estimates of its safety for older and different clinical groups of patients has been derived from ongoing monitoring through registries [27]. Should this new indication of use for the LVAD be approved, we would advocate early implementation of an LVAD database.

If REMATCH confirms the alternative hypothesis (ie, the LVAD confers a survival advantage), a logical next step for expanding the indications for mechanical circulatory assistance would be to use the LVAD as an alternative to cardiac transplantation. Directly comparing the LVAD with cardiac transplantation in a randomized manner presents challenging ethical and practical design problems. In particular, such a trial will be plagued by crossovers from LVAD to transplantation. Clearly, patients enrolled in a clinical trial and assigned to LVAD therapy cannot be expected to totally give up the option of cardiac transplantation. REMATCH, however, may mitigate this problem should the quality of life and survival observed be comparable to those seen with transplantation. If the experiences of both groups are comparable, patients should be more willing to stay with either assignment in a randomized design. Some people would argue that such an expansion of use should not require a randomized experiment but rather should rely on established survival and quality-of-life benchmarks. The drawback to that approach is that true comparability of treatment groups with respect to their prior risk of developing defined end points cannot be assured, and the credibility of the comparison would always be in question.

Cardiovascular medicine has established an impressive track record for the rigorous evaluation of new clinical interventions, which more recently has included quality-of-life end points as well as survival. Clearly, the assessment of new clinical procedures is a dynamic process; to an extent, its format reflects the interests of the health care system and the emergence of new stakeholders. Pressures for cost containment have fueled efforts to demonstrate value for money in the adoption of new procedures. Clinical trials like REMATCH, which incorporate the broader outcomes of cost, cost-effectiveness, and quality of life, may well become the paradigm for introducing new surgical procedures in years to come.

	Acknowledgments

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 
The REMATCH trial is supported in part by the National Institutes of Health, cooperative agreement HL-53986 from the National Heart, Lung, and Blood Institute, Bethesda, MD, and by funding from Thermo Cardiosystems Inc, Woburn, MA.

	Appendix 1. Exclusion criteria

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 

1. Cause of heart failure due to or associated with uncorrected thyroid disease, obstructive cardiomyopathy, pericardial disease, amyloidosis, or active myocarditis 2. Technical obstacles that pose an inordinately high surgical risk in the judgment of the certified surgeon 3. International normalized ratio > 1.3 or prothrombin time > 15 seconds within 24 hours before randomization 4. Body surface area < 1.5 m2 5. Body mass index > 40 kg/m2 6. Severe chronic obstructive pulmonary disease as evidenced by forced expiratory volume 1.5 L/min 7. If premenopausal, positive serum pregnancy test 8. Fixed pulmonary hypertension with pulmonary vascular resistance 8 Wood units that is unresponsive to pharmacologic intervention, documented within 90 days before randomization 9. Patient under consideration for conventional revascularization procedure, therapeutic valvular repair, left ventricular reduction procedure (ie, Battista), or cardiomyoplasty 10. History of cardiac transplantation, left ventricular reduction procedure, or cardiomyoplasty 11. Presence of implanted mechanical aortic valve that will not be converted to bioprosthesis at time of LVAD implantation 12. Evidence of intrinsic hepatic disease defined as liver enzyme values (aspartate aminotransferase, alanine aminotransferase, or total bilirubin) > five times the upper limit of normal within 4 days before randomization, or biopsy-proved liver cirrhosis 13. Occurrence of stroke within 90 days before randomization or history of cerebrovascular disease with major (> 80%) extracranial or carotid stenosis documented by Doppler study 14. Confirmation by neurologist of impairment of cognitive function, presence of Alzheimer’s disease or any other form of irreversible dementia, or both 15. Evidence of untreated abdominal aortic aneurysm 5 cm as measured by abdominal ultrasound within 30 days before randomization 16. Suspected or active systemic infection 48 hours before randomization 17. Platelet count 50 x 103/mm3 within 24 hours before randomization 18. Serum creatinine 3.5 mg/dL or regimen of long-term dialysis 19. Major peripheral vascular disease accompanied by pain on rest or leg ulceration 20. Receiving calcium-channel blocker (except amlodipine besylate) or type I (eg, quinidine, procainamide hydrochloride, disopyramide phosphate) or type III antiarrhythmic agent (eg, encainide hydrochloride, flecainide acetate, propafenone hydrochloride, moricizine hydrochloride) within 28 days before randomization 21. Abdominal operation planned 22. Recent history of psychiatric disease (including drug or alcohol abuse) that is likely to impair compliance with study protocol 23. Receiving therapy with investigational intervention or participating in another clinical study 24. Presence of condition other than heart failure that would limit survival to less than 3 years

	Appendix 2. Rematch investigators and sites

Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 

Principal Investigator: Eric A. Rose, MD Data and Clinical Coordinating Center: International Center for Health Outcomes and Innovation Research of Columbia University: Elizabeth Clifford, MPH, Deborah Davis Ascheim, MD, Annetine C. Gelijns, PhD, Anny Fernandez, Daniel F. Heitjan, PhD, Ronald M. Lazar, PhD, Ronald G. Levitan, BS, Paul Meier, PhD, Alan J. Moskowitz, MD, Milton Packer, MD, Nvala Ronan, BS, Peter A. Shapiro, MD, Anita R. Tierney, MPH, Alan D. Weinberg, MS, Deborah L. Williams, MPH Clinical Subcommittee: Lynne Warner Stevenson, MD, Harvard University, Walter P. Dembitsky, MD, University of California, San Diego Mortality and Morbidity Committee: J. Philip Kistler, MD, Harvard University, Val Jeevanundum, MD, University of Chicago, John O’Connelly, MD, Wayne State University Clinical Sites: Allegheny General Hospital, Pittsburgh, PA: Edward B. Savage, MD, Michael A. Mathier, MD, Kathleen L. Lockard, RN, MBA, George Magovern, Jr, MD Brigham and Women’s Hospital, Boston, MA: Gregory S. Couper, MD, Wendy Johnson, MD, Nancy Cummings, RN The Cleveland Clinic Foundation, Cleveland, OH: Patrick M. McCarthy, MD, Robert E. Hobbs, MD, Michael Yeager, RN Columbia-Presbyterian Medical Center, New York, NY: Mehmet C. Oz, MD, Donna M. Mancini, MD, Margaret A. Flannery, RN, Katharine A. Catanese, MSN Fairfax Hospital, Annandale, VA: Nelson A. Burton, MD, Andrew Keller, MD, Aaron G. Hill, CCP, Tonya Kraus, MSN LDS Hospital, Salt Lake City, UT: James W. Long, MD, PhD, Joseph Brent Muhlestein, MD, John D. Marks, PE, Scott C. Gardner, PA-C, Carl Nelson, RN, Jennifer Pitt, BS Loma Linda University Hospital, Loma Linda, CA: Steven R. Gundry, MD, Anees J. Razzouk, MD, Thomas J. Heywood, MD, Rachel Kroncke, NP Loyola University Medical Center, Maywood, IL: Bryan Foy, MD, Ellen Galbraith, RN, Martin G. Mullen, MD, Marianne Laff, RN Ochsner Medical Institutions, New Orleans, LA: Clifford H. Van Meter, MD, Mandeep Mehra, MD, Lindsay Kersker, RN, Patricia Uber, BS, Pharm Rush-Presbyterian-St. Luke’s Medical Center, Chicago, IL: William J. Piccione, Jr, MD, Maria Rosa Costanzo, MD, Annette Mattea, RN, Walter G. Kao, MD Sharp Memorial Hospital, San Diego, CA: Walter P. Dembitsky, MD, Brian E. Jaski, MD, Suzanne Chillcott, RN, BSN, Susan Harte, RN St. Luke’s Medical Center, Milwaukee, WS: Alfred T. Tector, MD, L. Samuel Wann, MD, Lynne M. Mathiak, RN, Tracey Graham, RN Temple University Hospital, Philadelphia, PA: Valluvan Jeevanandam, MD, Satoshi Furukawa, MD, Howard J. Eisen, MD, Joelle Hargraves, MSN Texas Heart Institute, Houston, TX: O. Howard Frazier, MD, James T. Willerson, MD, Edward A. Massin, MD, June Kolesar, BS, Timothy J. Myers, BS University of Alabama, Birmingham, AL: William L. Holman, MD, Robert C. Bourge, MD, Candace Wainscott, RN University of Iowa Hospitals and Clinics, Iowa City, IA: Wayne E. Richenbacher, MD, Ron Oren, MD, Kate C. Seemuth, MSA, Carolyn Laxson, RN, MA University of Michigan Hospital, Ann Arbor, MI: Francis D. Pagani, MD, PhD, Keith D. Aaronson, MD, Hillary M. Monaghan, RN University of Minnesota, Minneapolis, MN: Soon John Park, MD, Leslie W. Miller, MD, Sofia Ormaza, RN University of Washington Medical Center, Seattle, WA: Curtis William, MD, Daniel Fishbein, MD, Sandi Kruse, MN

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Top Abstract Introduction Randomized clinical trials in... REMATCH trial phases and... What will we learn... Acknowledgments Appendix 1. Exclusion criteria Appendix 2. Rematch... References

 

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