Editor's Note: Inspired by the Q&A's and Discussions so far, Robert Yezierski of the University of Florida, Gainesville, US, submitted the following essay outlinining his view of the scientific enterprise as it relates to chronic pain. Read his thoughts, and share your own by leaving a comment below.
There is little doubt that there have been far too many quiet moments when it comes to talking about the success of translational pain research. Over the past five years we have seen a number of articles explaining how good we are at discovery, and yet, over a period of nearly two decades, we have little to show for it in terms of clinical advances. Perhaps the most compelling commentary on this topic is the growing economic burden of pain and the staggering number of people, from young adults to the elderly, affected by chronic pain. These statistics beg the question that, if our research strategy is on the right track, then why are the economic and prevalence numbers escalating at a rate higher than at any time in history?
Given a not-so-successful track record in translational research, one is tempted to ask the question, “Are we really that stubborn?” or, as some have said, “Are we just smart people making dumb mistakes,” and working with the hope that if we keep plugging away we will eventually find a magic bullet? First, we need to appreciate the fact that when dealing with chronic pain there are no magic bullets. Second, we should acknowledge that our basic strategy of problem solving, starting with the development and assessment of preclinical models right through to the design of clinical trials, hasn’t changed much in 20 years. When one considers that all preclinical models of chronic pain produce exactly the behavioral effects desired, and that using these models we have gained a much improved understanding of the mechanisms responsible for different pain conditions, the obvious question is, why then, are things getting worse instead of better?
One possible answer is that for all the discoveries we have made studying pain in rodents there seems to be little evidence for meaningful parallels with the human condition. Several years ago an American Pain Society (APS) Task Force wanted to do a series of articles on translational research. Over a thirty year period the list of accomplishments was not very impressive, which led to the conclusion that part of the message should include a statement related to the question “How do we justify a research strategy based on doing the same thing over and over with expectations that we will achieve a different outcome?” Unfortunately the APS Bulletin was discontinued and the articles were never written but the message still remains that there is an overriding belief that we are on the right path in spite of the fact that for several decades there has been little progress in the development of effective new strategies for the long term treatment of chronic pain.
Before we get too carried away criticizing ourselves for the missteps we have taken perhaps we should take a look at the comments made by the panel of science advisors assembled by the Pain Research Forum. Interestingly, what we find are opinions on a number of different aspects of pain research, including the topic of translation. In some circles, the distance between bench research and bedside treatment has been labeled the “valley of death.” There are a number of reasons why this valley exists and the reasons are not that different today from what they were nearly a decade ago. In his discussion What is the Reason for Lack of Translation in the Pain Field, Jeffrey Mogil points out that there are potentially five reasons for our disappointing record in translational research, including: (1) lack of relevant pain models; (2) species differences between rodents and humans; (3) repeated failures of clinical trials; (4) regulatory barriers; and the fact that (5) pain is not unique, as translation is poor for nearly all neurological disorders.
The issue of relevance of pain models is taken to another level by Anne Louise Oaklander (in Patient-Centered Research: A Conversation With …) who states that one of the problems with animal models is that “it is not clear how relevant these models are.” Some models “don’t correspond to any particular human disease,” or correspond “loosely at best to any human disease or illness.” Instead of defending the validity and relevance of existing models, perhaps what we should be doing is looking at whether any substantial progress has been made in dealing with the conditions they are supposed to represent. Without question, preclinical scientists do a tremendous job dissecting and reducing problems to their fundamental components. We then create a story to explain behavioral modifications and identify therapeutic targets. Unfortunately, this is often done without confirmation from the human condition, which in the end may be the biggest contributing factor to the disappointing record of translation. The disappointments that have occurred far too frequently raise the question of how many times we need to experience the “next major breakthrough” only to have the entire concept disappear after a failed clinical trial. The list is long and unfortunately filled with discoveries that were supposed to lead to major advances in therapeutic intervention. Some would say it’s the nature of science, while others would say that we should learn from our misfortunes and make adjustments to the strategy we employ to accomplish our goals.
If we are to reverse the historical trend of failed translation, one strategy that makes a lot of sense is that expressed by Rohini Kuner (in From Patients to Signaling Pathways: A Conversation With …), who states that we need “to think first about what really happens in patients and then try to design pain models and experiments accordingly. It’s a reverse translation approach.” If we want to make real advances, then we have to look at what’s happening in patients and try to implement that in the questions we ask in animal models,” she says. The bottom line she says, is that we have “almost a moral obligation to stop and ask whether what we’re doing is really relevant, and if not, how can we make it more relevant.” In an effort to pursue discovery and build on previous work, we routinely look for parallels with previous animal research. This is a logical strategy but it we are interested in translation perhaps confirmation with the human condition would be far more beneficial. There is no denying that basic researchers excel at identifying and answering questions that play an integral role in increasing our understanding of disease, pathogenesis, and therapeutic mechanisms. The question we need to ask, however, is how much discovery is needed before it’s time to validate with clinical relevance.
Today our basic knowledge and understanding of pain mechanisms far exceeds what we imagined 30 years ago. Over the past three decades we have been rewarded with a rich collection of significant discoveries but have yet to produce an equal assortment of therapeutic advances that have lessened the financial burden of chronic pain or had an impact on the number of people affected by this condition. If our goal is to impact pain treatment then we need a better strategy that will create far more opportunities for effective intervention than the system currently in place. Although valuable from the standpoint of expanding our basic understanding, unfortunately the most fundamental questions that basic scientists answer are not always directly relevant to any prospective form of treatment or clinical advancement. Is it time to stop and ask whether we need more molecules, receptors, or signaling pathways to further enhance our understanding? Does a yes answer to this question get us closer to achieving successful translation? If history can be our guide perhaps we should take a long hard look at our track record before deciding how to proceed.
Based on what we know about the biology of pain, one could make a case that if all we had to deal with is the biology of pain, our strategy of pain management might be a lot more successful. Unfortunately, the psychosocial dimensions of pain are two additional components that play a major role in the pain experience. The fact that more effective pain management strategies have been largely elusive in spite of an increased understanding about the biology of pain could be pointing to the fact that the psychosocial components are far more important than previously realized. One could make the case that the biology of pain is important in the early onset or initiation of pain but in the transition to the chronic state the psychosocial components play an increasingly more prominent role. If that’s the case should we admit that pursuing the biology of pain has little chance of reversing the trend we are presently experiencing with the treatment of chronic pain and that perhaps we should turn our attention in another direction.
Such a change would require a major retooling of the research machine and a major adjustment in the mindset of the research community. Standing in the way of such a change is the fact that pain research is a big business. From the small corner of the National Institutes of Health responsible for pain research in the US, to professional societies, to faculty, postdocs and students engaged in pain research, to the hundreds of millions of R&D dollars invested by corporations, pain research represents an enormous financial commitment by the private, public and government sectors of our society. The system is designed for discovery and rewards novel research strategies but ironically ignores clinical relevance. If we look closely at the last 30 years it is clear that we have learned a lot about how rodents process and respond to pain, but it appears that this knowledge has helped us do little more than raise our hopes until we experience the failure of the next clinical trial.
One of the principal contributing factors to this ever expanding problem is that knowledge gained from basic science is assumed to be an end in itself rather than a means to achieve better patient care. The mentality that NIH grants are funded because of an elegant research design that is likely to provide insight and yield fundamental discoveries even if there is no prospect to produce something that helps the human condition must be part of the conversation when discussing reasons for failed translation. The NIH peer review system strongly favors hypothesis-driven basic research over applied research that is driven to develop more effective clinical treatments. If the success of translational research is going to change, something needs to change in a dramatic way and review panels will need to use different criteria to evaluate the merit of research proposals.
One of the ways to ensure the future success of translational research is for professional organizations (APS, IASP) to take the lead and promote to young investigators the need for innovative approaches with an emphasis on applied research with endpoints pointing towards a clinical objective. There is also a need to understand that the scale and complexity of today’s research problems demands that scientists move beyond their own discipline and explore new models of team science. The formula for achieving translational success is going to require basic and clinical scientists working collaboratively in relationships based on a mutual understanding established during their early years of professional development. Creating an interface between science and medicine will produce clinician-scientists as well as a new breed of scientist-clinicians that will recognize the necessity of keeping clinical application as the number one priority.
The discussion of how to resolve the challenges of translational research will no doubt continue. As it does we need to recognize the importance of stepping back and reflecting on where we have been and more importantly whether the strategy we are using to accomplish our goals makes sense or needs to be changed. There are a lot of places where changes could be made but whether we are prepared to pull the trigger and change the way we have traveled for more than 30 years remains to be seen. At the center of this decision is not the curiosities of the inquisitive scientist searching for the next discovery but the growing numbers of patients who have put their trust in those they believe are doing the right thing.