Discovery Versus Translation: Do we Need Different Strategies?

There is little doubt that we have experienced far too many quiet moments when it comes to talking about the success of translational pain research. Over the past 5 years a number of articles have been written explaining how good we are at preclinical discovery, and yet, over a period of nearly two decades, we have little to show for it in terms of significant clinical advances in the development of more effective interventions [1]. 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 [2,3]. These statistics beg the question: if our research strategy is on the right track, then why are the economic and prevalence metrics escalating at a rate faster than at any time in history and why are providers relying on the same basic drug classes to treat pain that have been in place for over a decade?

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 asked, “Are we just smart people making dumb mistakes?” working with the hope that if we keep plugging away we will eventually discover 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 significantly in 20 years. When one considers that all preclinical models of chronic pain reliably produce the desired behavioral effects, and that these models have provided a much improved understanding of the putative mechanisms responsible for different pain conditions, the obvious question is “why has not all the research productivity been validated with a positive clinical outcome?” One possible answer is that for all the discoveries we have made studying pain in rodents, there seems to be little evidence of meaningful parallels with the human condition. It is also possible that what we have been studying for the past 30 years applies primarily to acute pain and that all preclinical models are distant relatives to the more clinically relevant condition of chronic pain. One cannot avoid the unthinkable possibility that we might also be on the wrong track, asking the wrong questions, focusing on the wrong strategies, or in many areas of research doing nothing more than tweaking what is already a thorough understanding of the problem rather than asking questions that will take the conceptual understanding of pain to a level that will yield translational benefits. Based on the substantial gap between basic research and the development of novel interventions it was suggested that what is needed is a major paradigm shift in pain research [1]. This is probably not a bad strategy, but the reality is that research fields are not known for dramatic changes in direction. Any changes that occur are likely to be incremental and for this reason the future of pain research has a good chance of continuing to provide more breakthrough discoveries to justify the federal and private investment of resources, but unfortunately if history is any kind of benchmark there will only be small, if any, translational benefits.

Several years ago an American Pain Society Task Force was asked to do a series of articles on translational research. Over a 30-year period and hundreds of millions of research dollars, the list of accomplishments was not very impressive. This 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 methods and models that have failed to achieve our desired goals?” Unfortunately, the American Pain Society 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. Without question this is a sobering reality and perhaps partly responsible for the reluctance of legislators to provide an unending supply of resources to maintain or expand research initiatives.

Before we get too carried away criticizing ourselves for the missteps we have taken perhaps we should look at the comments of leading pain scientists for some insight and opinions on where we have gone wrong. In some circles, the distance between bench research and bedside treatment has been labeled the ‘valley of death‘ [4]. 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. Jeff Mogil points out that there are five potential reasons for our disappointing record in translational research, including: lack of relevant pain models; species differences between rodents and humans; repeated failures of clinical trials; regulatory barriers; and the fact that pain is not unique, as translation is poor for nearly all neurological disorders [101].

The issue of relevance of pain models is taken to another level by Anne Louise Oaklander who described the problem with animal models saying “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” [102]. 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 and then they 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 road to translation. The disappointments of the past have raised questions as to how many times we need to experience the excitement of the ‘next major breakthrough‘ only to have it quickly disappear after a failed clinical trial. The list is long and unfortunately filled with many discoveries that had enormous promise of providing new directions needed to develop innovative new strategies for the management of chronic pain. Some would say that this is the nature of science, while others would say 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 “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” [103]. “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.” The bottom line is 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” [103]. In an effort to pursue discovery and build on previous accomplishments we routinely reflect on historical parallels that provided the foundation for a specific field of study. This is a logical approach but if we are interested in translation perhaps validation with the human condition rather than confirmation of preclinical studies would be far more beneficial. There is no denying that basic researchers excel at identifying and answering questions that play an integral part in understanding disease and potential therapeutic mechanisms. The question we need to ask, however, is how much discovery is needed before it‘s time to validate with clinical relevance. Are the incremental advances in understanding providing the foundation for the therapeutic leap that is needed? At what point is it necessary to be accountable not only to the research entity we have created but also to those waiting patiently for therapeutic advances.

Few would argue that 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, to our disappointment, these have yet to produce an equal assortment of therapeutic milestones 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 change the landscape of pain treatment then what we need is a better strategy that will create a new level of understanding and more opportunities for developing more effective interventions. 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 form of treatment or clinical advancement. Is it time to stop and ask ourselves whether more molecules, channels, receptors, or signaling pathways are needed 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 basic biology of nociception, our current strategy of pain management might be a lot more successful. Unfortunately, the psychosocial, cognitive and affective dimensions of pain are additional components that play a major role in the pain experience. The fact that more effective management strategies for chronic pain have been largely elusive in spite of an increased understanding about the biology of pain could be pointing to the fact that the psychosocial and affective components of pain are far more important than previously realized. One could make the case that the biology of pain is important in the initial stages of acute pain but in the transition to the chronic state the psychosocial and affective components play an increasingly more prominent role. If that‘s the case should we consider the possibility that pursuing the biology of pain has little chance of reversing the trend we are presently experiencing? Perhaps we should turn our attention in another direction. Such a change would require a major retooling of the research machine and major adjustments in the mindset of the research community. Standing in the way of such a change is the fact that pain research is big business. From the small corner of the NIH, to professional societies, to faculty, postdoctoral trainees and students engaged in pain research, to the hundreds of millions of research and development dollars invested by corporations, the field of pain research encompasses a significant financial commitment by the public, private and government sectors of our economy. One must also consider the fact that pain impacts our economy to the tune of over US$600 billion per year which some have pointed out makes the trickle-down effect of pain very profitable to many segments of the economy.

At present, our current system of research 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. Unfortunately, each major breakthrough and leap of knowledge raises our hopes but has failed to deliver anything that providers believe equates to a similar breakthrough in their ability to treat patients. One of the principal contributing factors to this ever-expanding problem is that knowledge gained from basic science is assumed to be a means to achieve better patient care. There is a mentality that NIH grants should be funded because of an elegant research design that is likely to provide insight and yield fundamental discoveries that will ultimately translate into something beneficial to the human condition. The fallacy of this argument 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 driven to develop more effective clinical treatments. If the success of translational research is going to change review panels should consider using different criteria to evaluate the merit of research proposals. Do we need a separate set of criteria for ‘discovery‘- versus ‘translation‘-based proposals? Such a solution would encourage a different type of innovation and creativity that potentially could pay significant dividends. Whatever the solution the fact is the current system is not working and changes are needed.

One of the ways to ensure the future success of translational research is for professional organizations (e.g., the American Pain Society and the International Association for the Study of Pain) to take the lead and encourage young investigators to consider the need for innovative approaches with an emphasis on applied research with end points pointing towards clinical objectives. 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 the clinic will produce clinician–scientists as well as a new breed of scientist anxious to partner with clinicians who recognize the necessity of keeping clinical application a 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 has met our needs. There are a lot of places where changes could be made but whether we are prepared to make these changes or if we are securely committed to the road we have traveled for more than 30 years remains to be seen. At the center of this decision is not the need to satisfy the curiosity of the inquisitive scientist searching for the next discovery. On the contrary, what must be the driving force is the growing numbers of patients who have put their trust in those they believe are doing the right thing.

Acknowledgements

The author thanks the editorial staff of the Pain Research Forum for their permission to edit and publish this editorial, which first appeared as a commentary on the Pain Research Forum website (www.painresearchforum.org).

Financial & competing interests disclosure

The author has no relevant affiliations or financial involvement with any organization or entity with a financial interest in or financial conflict with the subject matter or materials discussed in the manuscript. This includes employment, consultancies, honoraria, stock ownership or options, expert testimony, grants or patents received or pending, or royalties.

No writing assistance was utilized in the production of this manuscript.