The impossible task of developing a new treatment for heart failure

Abstract

As I complete my 2-year tenure as president of the Heart Failure Society of America, I was asked by the editor of the Journal of Cardiac Failure to write an editorial about a major development or issue has had a significant impact on our field. One of the most important events during the past 2 years has been the repeated failure of new therapies for heart failure to fulfill their original promise to improve the management of this disease. The disappointing results in recent large-scale clinical trials have important implications for science, patients, industry, and our society.It was not that long ago when we thought we understood the syndrome of heart failure. One hundred years ago, we believed it to be primarily an edematous disorder; 30 years ago, we declared it to be a hemodynamic derangement; and 10 to 15 years ago, we were convinced it was principally a neurohormonal event. In all three instances, we were right—and we were wrong. Heart failure is a circulatory disorder characterized by abnormalities in the control of sodium balance, cardiac function, and neurohormonal activation; clinical improvement can follow the use of drugs that can ameliorate these derangements (diuretics, digitalis, angiotensin converting-enzyme [ACE] inhibitors, and β-blockers). Yet, despite substantial advances in our understanding and management of heart failure, we have had few successes and many failures. Nearly 1,000 new drugs and devices have been developed for the treatment of heart failure during the past 20 years, but only 9 have received regulatory approval and are being used in the clinical setting. Most of our efforts to correct fluid retention, stimulate the inotropic state of the heart, and modulate neurohormonal systems have not predictably improved the condition of patients with heart failure.Recent experiences have reinforced our frustration. In large-scale trials completed during the past 18 months, the addition of endothelin antagonists, cytokine antagonists, and angiotensin II receptor antagonists to patients with heart failure already receiving an ACE inhibitor and β-blocker produced little incremental benefit and (in some cases) appeared to have been harmful. Thousands of patients were enrolled in these trials, hundreds of investigators and coordinators worked hard to move them to completion, yet none produced a persuasively favorable result. How could our expectations for these new treatments have been so wrong? Before these trials were launched, the mechanisms underlying the anticipated benefit of the new drugs had been clearly defined and seemed scientifically valid; studies of the drugs in experimental models of heart failure produced dramatic improvements; and early clinical trials in hundreds of patients yielded extremely encouraging results. We realized that preliminary data could be misleading, but the early results with these new drugs looked better than the early results with even ACE inhibitors and β-blockers. It seemed reasonable to believe that at least one of these promising drugs should have succeeded. Yet, when the final results became available, not one of these drugs fulfilled its original promise.To complicate matters further, the analytical methods that we use to interpret the results of clinical trials have made it difficult to know what conclusions are warranted. During the past 20 years, a set of statistical principles have been developed to guide the interpretation of clinical trials and to protect clinicians from reaching favorable conclusions from data that show a positive result only because of the play of chance. Yet, in recent years, such principles have contributed importantly to the frustration experienced by researchers involved in the conduct of clinical trials of new agents for the treatment of heart failure. For example, a large-scale, placebo-controlled trial of valsartan in more than 5,000 patients with heart failure (Val-HeFT) achieved one of its primary endpoints (the combined risk of death and hospitalization for heart failure), which should have led to the conclusion that valsartan would be useful if added to conventional therapy for heart failure. However, a subgroup analysis suggested that valsartan might be harmful if added to ACE inhibitors and β-blockers, two classes of drugs that should be the cornerstone of conventional therapy for most patients. Should this subgroup analysis be believed? Statisticians would caution us not to become too excited by subgroup analyses, but this apparent interaction was hard to ignore. As a result, the investigators failed to convince the community about their original hypothesis—even though the trial achieved its primary objective.In another recent example, a large-scale trial that compared omapatrilat with enalapril in more than 5,000 patients with heart failure (OVERTURE) failed to achieve its primary endpoint (the combined risk of death and hospitalization for heart failure), which led to the conclusion that omapatrilat offered no advantage over a conventional ACE inhibitor for the treatment of heart failure. However, after the trial was completed, the investigators noticed that the protocol had defined the primary endpoint so as to include only hospitalizations for heart failure requiring intravenous therapy; yet the protocol had also designated the SOLVD Treatment Trial as the reference standard, which included all hospitalizations of heart failure regardless of the need for intravenous medication. When the trial was reanalyzed using the definition for hospitalization for heart failure used in the reference standard, the results achieved statistical significance on the primary endpoint. Should this retrospective analysis be believed? Statisticians would caution us not to become too excited by post hoc reanalyses, but it is hard to conclude that the trial found no difference between the two drugs. Hence, even though the Val-HeFT and OVERTURE trials were the largest studies ever conducted with new drugs for the treatment of heart failure, neither succeeded in clarifying the appropriate role for the new drugs in the management of this disorder.If we really want to become very depressed, we could survey our accomplishments during the past 20 years and realize that we have not yet succeeded in developing a single drug for the long-term treatment of heart failure that was prospectively designed to correct an identifiable physiologic abnormality known to be present in the disorder. ACE inhibitors, β-blockers, and spironolactone were not developed to address the neurohormonal abnormalities of heart failure. They were formulated for the treatment of other cardiovascular diseases (e.g., hypertension, angina, edema) and evaluated for the treatment of heart failure as an afterthought—frequently with great hesitation and reluctance on the part of the sponsors and generally accompanied by great skepticism from the scientific community. Such a perspective should certainly make us wonder: if these drugs were not already established for some other indication, would anyone have pursued their potential utility for the treatment of heart failure? If our most effective agents were developed for heart failure only because they were effective for some other condition, how likely are we to generate support for the development of new drugs that work only for heart failure?Some would look back at all of these disappointments and conclude that the present state of affairs is the direct result of our profound ignorance of the mechanisms that led to the development and progression of heart failure. What is needed, they would argue, is a renewed commitment to basic research in an effort to understand what is really happening in the failing heart. Such a perspective is hard to challenge; we can never be criticized too severely for professing our ignorance. Yet such a view ignores an important aspect of the story: The recent failures did not come early in the development of these new drugs but occurred very late in the process—after their sponsors (convinced that the new drug had a high likelihood of success) had exposed thousands of patients to an experimental treatment and spent hundreds of millions of dollars on the conduct of large-scale trials. So we are not simply suffering from a lack of good science, we also are terribly handicapped by the absence of a reliable way of predicting the success of a new drug before a major commitment is made to its development. Until we are better able to identify candidates with a reasonable chance of success, sponsors will be understandably reluctant to commit the vast resources needed for regulatory approval and clinical acceptance.Unfortunately, the ability to translate good science into a clinical reality is likely to become particularly challenging in the future. In the past, drugs that were developed for the treatment of heart failure exerted an effect that we could easily measure (e.g., ACE inhibitors lowered blood pressure, β-blockers slowed heart rate). These physiologic changes may have had little to do with how these drugs actually worked in patients with heart failure, but at least they provided the basis—even if unreliable—of determining the dose that might be evaluated in a clinical trial. In the future, however, new drugs may have uniquely specific targets (e.g., a drug may modify the expression of a single gene in the heart in a way that is associated with no other measurable effect). How does one determine the dose of such an agent? The situation is complicated further by the fact that—if the purpose of influencing the gene is to slow the loss of cardiac cells—the only endpoint that can reflect the benefit of treatment is survival. As a result, the sponsor interested in developing such a drug for the treatment of heart failure faces the nearly impossible challenge of carrying out a large-scale mortality trial to gain regulatory approval and having to do so without being able to know the appropriate dose or having reasonable assurance that the drug is exerting some effect that can be measured in patients. Therefore, if anyone ever meets the extraordinarily difficult scientific challenge of developing a gene-based therapy for the treatment for heart failure, he or she would then have to face the extraordinarily difficult task of proving that it works.Given these nearly impossible hurdles to the successful development of a new drug for heart failure, some investigators appear to have simply given up on pharmacologic interventions altogether. Their reasoning seems logical enough: The development of new drugs is simply too hard, the uncertainty too great, and the likelihood of success too small—not to mention the possibility of unexpected side effects. Drugs always exert potentially undesirable effects that cannot be anticipated, and attempts to identify a dose that limits such effects while still producing a therapeutic response represent nothing more than a guessing game. Understandably frustrated by recent experiences, such investigators have turned to the development of devices for the management of heart failure. By their very nature, devices can exert a specific effect in a highly selective manner and in a way that can be readily measured. As a result, enthusiasm for the development of new devices for heart failure is soaring. Devices have been created that bypass conduction defects, resynchronize the heart, modify the process of cardiac remodeling, and terminate potentially lethal rhythm disturbances.Do devices represent the future of new treatments for heart failure? Our colleagues in electrophysiology would think so; they enthusiastically embraced the development of devices years ago when they became frustrated by the numerous failures of antiarrhythmic drug treatment. However, many appear to be reluctant to follow this path, given that the development and commercialization of devices carries with it as many challenges as the development of drugs. The field of clinical trials with cardiac devices for heart failure is still in its infancy, and both investigators and regulatory agencies struggle in their attempts to establish the principles that could reasonably be used to govern the evaluation of devices. What endpoints should be used? What controls are appropriate? How can one use symptomatic measures of efficacy when both investigators and patients are likely to know who has received a device and are likely to be influenced by such knowledge? One approach is to require devices to meet the same standards as drugs (i.e., that all devices should be evaluated to determine their effect on survival). Such a requirement exists for drugs because of fears that drugs may increase the risk of death; such a requirement may also be appropriate for devices because all-cause mortality is not likely to be influenced by knowledge of the assigned treatment, and it accounts for the initial risk of inserting the device into the patient. Yet, even if a new device were to be deemed effective and approved, we would still need to deal with the fact that the placement of such devices will require an expertise beyond that possessed by most physicians who care for patients with heart failure and generate an expense beyond the resources of most organizations responsible for covering the costs of health care.The ultimate manifestation of the frustration experienced by those developing new treatments for heart failure is the growing interest in cardiac assistance or replacement therapy. Advocates for such an approach would argue: Why spend a lifetime trying to determine what is wrong with the failing heart and developing a new approach to treatment based on such understanding? Not only will we fail in the effort, they would argue, but even if we could discover what was wrong and could develop a way of correcting the problem, it would be difficult to prove that the new treatment worked to the satisfaction of regulatory authorities and clinicians. Perhaps we should manage broken hearts the way that we manage other mechanical problems (broken cars and refrigerators) in our daily lives. We do not try to figure out what went wrong; we simply replace them (in part or in whole). Indeed, cardiac replacement or mechanical assistance has enormous appeal, but it is important to recognize that it is fundamentally an anti-intellectual approach. Its advocates would certainly not be distressed by such criticism. Instead, they would emphasize that the real objective is not to understand heart failure but to make patients with heart failure feel better and live longer. An effective device would do that, they would argue, and the expected benefits would be so enormous that a clinical trial would be both unnecessary and unethical—or at the very least, not very large. We can only hope that they are right, because our patients certainly need all of the help that they can get. However, during the past 20 to 30 years, far more lives have been improved and saved because of the development of new drugs than because of advances in cardiac replacement or assistance. It may be true—as shown in a recent randomized trial (REMATCH)—that placement of a left ventricular assist device prolongs life. However, the costs of delivering such therapy are extraordinary and the rate of serious complications is extremely high—all to achieve a barely discernible difference in mortality after 2 years.Given the almost insurmountable challenges that we face in developing a new treatment for heart failure, what should we do? Should we surrender to our sense of futility and declare the era of innovation in heart failure to be over? No one would advocate such a stance. It is true that we might develop only one new major advance in the treatment of heart failure every decade, but that would be better than no new treatments. Yet, while we wait for the next advance, there is something important we can all do. We can make sure that patients with heart failure are receiving the interventions that we are confident help to improve both the quality and quantity of their lives. Why develop a new treatment if only 10% to 20% of patients receive it? Promoting the education of both physicians and patients about advances in heart failure management is an essential step in fulfilling the promise created by any new and effective intervention. If we prove a new intervention works but no one receives it, we have achieved only a sterile intellectual milestone that has little impact on public health. However, if we develop effective ways of expanding the acceptance of an established treatment, we may not advance our understanding of mechanisms, but we will be helping patients. That is the most important thing we can do while we wait for the next advance in the field.Expanding the acceptance of established treatments through the education of patients and physicians is one of the primary goals of the Heart Failure Society of America—an objective that has been strongly reinforced during my tenure as president. I expect that these efforts will continue and grow in the coming years as we fulfill our mission to have a major impact on this important public health problem. As I complete my 2-year tenure as president of the Heart Failure Society of America, I was asked by the editor of the Journal of Cardiac Failure to write an editorial about a major development or issue has had a significant impact on our field. One of the most important events during the past 2 years has been the repeated failure of new therapies for heart failure to fulfill their original promise to improve the management of this disease. The disappointing results in recent large-scale clinical trials have important implications for science, patients, industry, and our society. It was not that long ago when we thought we understood the syndrome of heart failure. One hundred years ago, we believed it to be primarily an edematous disorder; 30 years ago, we declared it to be a hemodynamic derangement; and 10 to 15 years ago, we were convinced it was principally a neurohormonal event. In all three instances, we were right—and we were wrong. Heart failure is a circulatory disorder characterized by abnormalities in the control of sodium balance, cardiac function, and neurohormonal activation; clinical improvement can follow the use of drugs that can ameliorate these derangements (diuretics, digitalis, angiotensin converting-enzyme [ACE] inhibitors, and β-blockers). Yet, despite substantial advances in our understanding and management of heart failure, we have had few successes and many failures. Nearly 1,000 new drugs and devices have been developed for the treatment of heart failure during the past 20 years, but only 9 have received regulatory approval and are being used in the clinical setting. Most of our efforts to correct fluid retention, stimulate the inotropic state of the heart, and modulate neurohormonal systems have not predictably improved the condition of patients with heart failure. Recent experiences have reinforced our frustration. In large-scale trials completed during the past 18 months, the addition of endothelin antagonists, cytokine antagonists, and angiotensin II receptor antagonists to patients with heart failure already receiving an ACE inhibitor and β-blocker produced little incremental benefit and (in some cases) appeared to have been harmful. Thousands of patients were enrolled in these trials, hundreds of investigators and coordinators worked hard to move them to completion, yet none produced a persuasively favorable result. How could our expectations for these new treatments have been so wrong? Before these trials were launched, the mechanisms underlying the anticipated benefit of the new drugs had been clearly defined and seemed scientifically valid; studies of the drugs in experimental models of heart failure produced dramatic improvements; and early clinical trials in hundreds of patients yielded extremely encouraging results. We realized that preliminary data could be misleading, but the early results with these new drugs looked better than the early results with even ACE inhibitors and β-blockers. It seemed reasonable to believe that at least one of these promising drugs should have succeeded. Yet, when the final results became available, not one of these drugs fulfilled its original promise. To complicate matters further, the analytical methods that we use to interpret the results of clinical trials have made it difficult to know what conclusions are warranted. During the past 20 years, a set of statistical principles have been developed to guide the interpretation of clinical trials and to protect clinicians from reaching favorable conclusions from data that show a positive result only because of the play of chance. Yet, in recent years, such principles have contributed importantly to the frustration experienced by researchers involved in the conduct of clinical trials of new agents for the treatment of heart failure. For example, a large-scale, placebo-controlled trial of valsartan in more than 5,000 patients with heart failure (Val-HeFT) achieved one of its primary endpoints (the combined risk of death and hospitalization for heart failure), which should have led to the conclusion that valsartan would be useful if added to conventional therapy for heart failure. However, a subgroup analysis suggested that valsartan might be harmful if added to ACE inhibitors and β-blockers, two classes of drugs that should be the cornerstone of conventional therapy for most patients. Should this subgroup analysis be believed? Statisticians would caution us not to become too excited by subgroup analyses, but this apparent interaction was hard to ignore. As a result, the investigators failed to convince the community about their original hypothesis—even though the trial achieved its primary objective. In another recent example, a large-scale trial that compared omapatrilat with enalapril in more than 5,000 patients with heart failure (OVERTURE) failed to achieve its primary endpoint (the combined risk of death and hospitalization for heart failure), which led to the conclusion that omapatrilat offered no advantage over a conventional ACE inhibitor for the treatment of heart failure. However, after the trial was completed, the investigators noticed that the protocol had defined the primary endpoint so as to include only hospitalizations for heart failure requiring intravenous therapy; yet the protocol had also designated the SOLVD Treatment Trial as the reference standard, which included all hospitalizations of heart failure regardless of the need for intravenous medication. When the trial was reanalyzed using the definition for hospitalization for heart failure used in the reference standard, the results achieved statistical significance on the primary endpoint. Should this retrospective analysis be believed? Statisticians would caution us not to become too excited by post hoc reanalyses, but it is hard to conclude that the trial found no difference between the two drugs. Hence, even though the Val-HeFT and OVERTURE trials were the largest studies ever conducted with new drugs for the treatment of heart failure, neither succeeded in clarifying the appropriate role for the new drugs in the management of this disorder. If we really want to become very depressed, we could survey our accomplishments during the past 20 years and realize that we have not yet succeeded in developing a single drug for the long-term treatment of heart failure that was prospectively designed to correct an identifiable physiologic abnormality known to be present in the disorder. ACE inhibitors, β-blockers, and spironolactone were not developed to address the neurohormonal abnormalities of heart failure. They were formulated for the treatment of other cardiovascular diseases (e.g., hypertension, angina, edema) and evaluated for the treatment of heart failure as an afterthought—frequently with great hesitation and reluctance on the part of the sponsors and generally accompanied by great skepticism from the scientific community. Such a perspective should certainly make us wonder: if these drugs were not already established for some other indication, would anyone have pursued their potential utility for the treatment of heart failure? If our most effective agents were developed for heart failure only because they were effective for some other condition, how likely are we to generate support for the development of new drugs that work only for heart failure? Some would look back at all of these disappointments and conclude that the present state of affairs is the direct result of our profound ignorance of the mechanisms that led to the development and progression of heart failure. What is needed, they would argue, is a renewed commitment to basic research in an effort to understand what is really happening in the failing heart. Such a perspective is hard to challenge; we can never be criticized too severely for professing our ignorance. Yet such a view ignores an important aspect of the story: The recent failures did not come early in the development of these new drugs but occurred very late in the process—after their sponsors (convinced that the new drug had a high likelihood of success) had exposed thousands of patients to an experimental treatment and spent hundreds of millions of dollars on the conduct of large-scale trials. So we are not simply suffering from a lack of good science, we also are terribly handicapped by the absence of a reliable way of predicting the success of a new drug before a major commitment is made to its development. Until we are better able to identify candidates with a reasonable chance of success, sponsors will be understandably reluctant to commit the vast resources needed for regulatory approval and clinical acceptance. Unfortunately, the ability to translate good science into a clinical reality is likely to become particularly challenging in the future. In the past, drugs that were developed for the treatment of heart failure exerted an effect that we could easily measure (e.g., ACE inhibitors lowered blood pressure, β-blockers slowed heart rate). These physiologic changes may have had little to do with how these drugs actually worked in patients with heart failure, but at least they provided the basis—even if unreliable—of determining the dose that might be evaluated in a clinical trial. In the future, however, new drugs may have uniquely specific targets (e.g., a drug may modify the expression of a single gene in the heart in a way that is associated with no other measurable effect). How does one determine the dose of such an agent? The situation is complicated further by the fact that—if the purpose of influencing the gene is to slow the loss of cardiac cells—the only endpoint that can reflect the benefit of treatment is survival. As a result, the sponsor interested in developing such a drug for the treatment of heart failure faces the nearly impossible challenge of carrying out a large-scale mortality trial to gain regulatory approval and having to do so without being able to know the appropriate dose or having reasonable assurance that the drug is exerting some effect that can be measured in patients. Therefore, if anyone ever meets the extraordinarily difficult scientific challenge of developing a gene-based therapy for the treatment for heart failure, he or she would then have to face the extraordinarily difficult task of proving that it works. Given these nearly impossible hurdles to the successful development of a new drug for heart failure, some investigators appear to have simply given up on pharmacologic interventions altogether. Their reasoning seems logical enough: The development of new drugs is simply too hard, the uncertainty too great, and the likelihood of success too small—not to mention the possibility of unexpected side effects. Drugs always exert potentially undesirable effects that cannot be anticipated, and attempts to identify a dose that limits such effects while still producing a therapeutic response represent nothing more than a guessing game. Understandably frustrated by recent experiences, such investigators have turned to the development of devices for the management of heart failure. By their very nature, devices can exert a specific effect in a highly selective manner and in a way that can be readily measured. As a result, enthusiasm for the development of new devices for heart failure is soaring. Devices have been created that bypass conduction defects, resynchronize the heart, modify the process of cardiac remodeling, and terminate potentially lethal rhythm disturbances. Do devices represent the future of new treatments for heart failure? Our colleagues in electrophysiology would think so; they enthusiastically embraced the development of devices years ago when they became frustrated by the numerous failures of antiarrhythmic drug treatment. However, many appear to be reluctant to follow this path, given that the development and commercialization of devices carries with it as many challenges as the development of drugs. The field of clinical trials with cardiac devices for heart failure is still in its infancy, and both investigators and regulatory agencies struggle in their attempts to establish the principles that could reasonably be used to govern the evaluation of devices. What endpoints should be used? What controls are appropriate? How can one use symptomatic measures of efficacy when both investigators and patients are likely to know who has received a device and are likely to be influenced by such knowledge? One approach is to require devices to meet the same standards as drugs (i.e., that all devices should be evaluated to determine their effect on survival). Such a requirement exists for drugs because of fears that drugs may increase the risk of death; such a requirement may also be appropriate for devices because all-cause mortality is not likely to be influenced by knowledge of the assigned treatment, and it accounts for the initial risk of inserting the device into the patient. Yet, even if a new device were to be deemed effective and approved, we would still need to deal with the fact that the placement of such devices will require an expertise beyond that possessed by most physicians who care for patients with heart failure and generate an expense beyond the resources of most organizations responsible for covering the costs of health care. The ultimate manifestation of the frustration experienced by those developing new treatments for heart failure is the growing interest in cardiac assistance or replacement therapy. Advocates for such an approach would argue: Why spend a lifetime trying to determine what is wrong with the failing heart and developing a new approach to treatment based on such understanding? Not only will we fail in the effort, they would argue, but even if we could discover what was wrong and could develop a way of correcting the problem, it would be difficult to prove that the new treatment worked to the satisfaction of regulatory authorities and clinicians. Perhaps we should manage broken hearts the way that we manage other mechanical problems (broken cars and refrigerators) in our daily lives. We do not try to figure out what went wrong; we simply replace them (in part or in whole). Indeed, cardiac replacement or mechanical assistance has enormous appeal, but it is important to recognize that it is fundamentally an anti-intellectual approach. Its advocates would certainly not be distressed by such criticism. Instead, they would emphasize that the real objective is not to understand heart failure but to make patients with heart failure feel better and live longer. An effective device would do that, they would argue, and the expected benefits would be so enormous that a clinical trial would be both unnecessary and unethical—or at the very least, not very large. We can only hope that they are right, because our patients certainly need all of the help that they can get. However, during the past 20 to 30 years, far more lives have been improved and saved because of the development of new drugs than because of advances in cardiac replacement or assistance. It may be true—as shown in a recent randomized trial (REMATCH)—that placement of a left ventricular assist device prolongs life. However, the costs of delivering such therapy are extraordinary and the rate of serious complications is extremely high—all to achieve a barely discernible difference in mortality after 2 years. Given the almost insurmountable challenges that we face in developing a new treatment for heart failure, what should we do? Should we surrender to our sense of futility and declare the era of innovation in heart failure to be over? No one would advocate such a stance. It is true that we might develop only one new major advance in the treatment of heart failure every decade, but that would be better than no new treatments. Yet, while we wait for the next advance, there is something important we can all do. We can make sure that patients with heart failure are receiving the interventions that we are confident help to improve both the quality and quantity of their lives. Why develop a new treatment if only 10% to 20% of patients receive it? Promoting the education of both physicians and patients about advances in heart failure management is an essential step in fulfilling the promise created by any new and effective intervention. If we prove a new intervention works but no one receives it, we have achieved only a sterile intellectual milestone that has little impact on public health. However, if we develop effective ways of expanding the acceptance of an established treatment, we may not advance our understanding of mechanisms, but we will be helping patients. That is the most important thing we can do while we wait for the next advance in the field. Expanding the acceptance of established treatments through the education of patients and physicians is one of the primary goals of the Heart Failure Society of America—an objective that has been strongly reinforced during my tenure as president. I expect that these efforts will continue and grow in the coming years as we fulfill our mission to have a major impact on this important public health problem.