Challenges of translating epidemiologic research: An application to rheumatic and musculoskeletal disorders

Abstract

Translation of research into public health policy is featured in common definitions of epidemiology, as an end result of scientific discovery on disease occurrence and causes. This dual nature of epidemiology, which brings together discovery and its use, seems to imply two main dimensions by which to judge epidemiologic research: technical or field-specific quality and societal value. This paper uses our research on the epidemiology of rheumatic and musculoskeletal disorders as a starting point to discuss the interface between these dimensions, exploring a number of conceptual, practical and ethical challenges that epidemiologists increasingly need to address when aiming for research translation. Those include not only the appraisal of the technical quality of research, which is familiar to researchers, but also the judgement on the usefulness and actual use of knowledge, as well as the assessment of the legitimacy of research based on translation potential. Several challenges lie ahead, but interdisciplinary conceptual and technical developments have the potential to guide future epidemiologic research of consequence. Approaches that recognize complexity and formalize the involvement of stakeholders in the research process within transparent frameworks open promising avenues for an effective translation of epidemiologic research projected into the future.

Background

Early on in their training, epidemiologists become familiar with a widely adopted definition of epidemiology as a discipline that aims to 1) study the occurrence and determinants of health states and 2) apply that knowledge to improve population health [1]. This definition sets wide boundaries for epidemiology, which in addition to pursuing scientific discovery is also expected – by definition – to have societal impact. This dual role has been a topic of discussion among epidemiologists for decades, as exemplified in the following two excerpts:

[…] even astrophysicists, whose work seldom induces engineering breakthroughs, can now pursue knowledge for its own sake without fear of being badgered about the practical relevance of their work. What physicists have gained, however, epidemiologists seem to have lost. Accusations have been mounting that epidemiologists have abandoned their public-health mission of being “physician-scientist” to society in favour of studying the scientific arcana of disease causation. […] epidemiologists are not social engineers; they are public-health scientists who have a right to specialise as they see fit. They should be free to choose the subject of their inquiries, whether it be social causes or molecular causes of disease. In: Rothman KJ, et al. Lancet, 1998. [2]

It is as if the house is burning down, but we are focussing on developing better theories on how to change the light bulb. […] Perhaps the nadir of this purist approach came when those who were trying to restore the population perspective to epidemiology, and to broaden its vision, were condemned as social activists by Rothman and colleagues in an influential paper in the Lancet. To let the methods determine the questions that are asked, and to ignore other important public health problems because they do not fit the paradigm, is not only bad public health practice but is also bad science. […] issues, like climate change or poverty, do not fit the paradigm at all (you need at least two planets!), and are therefore ‘someone else's problem.’ In: Pearce N. Int J Epidemiol, 2007. [3]

The extent to which epidemiologic research should – or is equipped to – address the issues that have the most relevance at the societal level remains an issue of current discussion in the epidemiologic literature [4,5]. In this paper, we use examples from our research on the epidemiology of rheumatic and musculoskeletal disorders to discuss specific challenges on the interface between the technical quality of research, i.e. the extent to which it can be considered scientifically valid, and its usefulness, i.e. the extent to which it may be expected to have a direct impact on society. We then explore different approaches that may be used to bring together those two dimensions. In this context we use the term translation as proposed by Szklo, to mean the “effective transfer of new knowledge from epidemiologic studies into the planning of population-wide and individual-level disease control programs and policies” [6].

The issue of technical (field-specific) quality

Historically, the main defining feature of epidemiology has been its blending of population thinking and group comparisons in an integrated theory [7]. Since there are numerous limits to the applicability of randomized controlled trials, causal inference in epidemiology relies mostly on observational approaches. Causal inference from observational data has shaped the history of epidemiology, fueling the development of theoretical frameworks and methods to deal with (non)comparability. This is much less of a concern in experimental designs, where the ceteris paribus condition can be a reasonable assumption. Field-specific discussions in epidemiology typically revolve around validity and its threats: bias, confounding and, arguably to a lesser extent, imprecision. The goal to produce knowledge of technical quality, i.e. valid conclusions about health states and their causes, is patent in well-known works throughout the history of epidemiology, e.g. [[8], [9], [10], [11], [12]], much more so than the technical tools needed to achieve an effective translation. Likewise, education and training programs for epidemiologists typically aim to provide a set of competences that fuel the conduct of research of technical quality, both in terms of the degree to which a study is free from bias or systematic error, usually termed internal validity, and of its generalizability to external populations, typically called external validity. The second part of the definition of epidemiology, i.e. the application of knowledge to change reality, has not been a fundamental component of the standard epidemiologist's toolkit. By training – and probably by inclination – scientists tend to judge research on the basis of field-specific quality, which includes intangible dimensions such as originality and inventiveness as well as more tangible dimensions related to methodological quality as defined above. The pursuit of technical quality seems to be a major driving force over the eras, with the process of translation being frequently seen by researchers as secondary to that of discovery in itself. Below we discuss specific reasons that may account for gaps between epidemiologic research and translation, through an epidemiologist's lens. For transparency, I will focus on our own research in the field of rheumatic and musculoskeletal disorders.

Gaps between field-specific quality and translation

Evidence in context: the example of adiposity and bone mass

Fragility fractures are frequent causes of death and impairment. Of all the evidence produced on the causes of bone fragility, arguably the most consistently reported besides age is body size. Doctors are well aware of the slender stereotype among patients with osteoporosis [13] and, at the population level, larger individuals have on average higher bone mass [14]. A strong statistical dependence between body size and bone mass has been a recurrent finding also in our research. We have observed this through direct relations between bone mass or density in children or adolescents and: a) different body size measures (weight, lean mass, fat mass and BMI) [15], b) total weight gain since birth up to age 6 [16], c) growth velocity in childhood [17], d) maternal and paternal adult BMI, e) maternal prepregnancy BMI, and f) maternal gestational weight gain [18]. We observed similar relations in adults, when examining bone mineral density at the hip, lumbar spine and forearm [19], and ultimately fragility fractures [20]. These findings are robust to different exposures (complementary body size and composition measures), different outcomes (crude and size-corrected bone mineral density and content), different study designs (cross-sectional and prospective), different analytical approaches (including different confounding structures and sensitivity analyses to deal with bias), and different stages of life. Importantly, they are consistent with theoretical models of biomechanical bone regulation [21] as well as with the existing body of empirical evidence. Globally, it seems reasonable to conclude that the relation we have repeatedly found between body size and bone mass is internally valid, in the sense that it is not likely explained by bias alone. Also, it has been replicated in different populations and settings, which supports its external validity. Using technical criteria alone, our findings seem robust and, if the prevention of fragility fractures is seen as a goal in isolation, it is tempting to frame them through the lens of intervention or policy. Despite that, the translation of such a finding into public policy goes far beyond the technical issue of causal inference or the goal of fragility fracture prevention, and should be seen as part of a much more complex public health system. In view of the overwhelming evidence on the harms of excess adiposity on a variety of health outcomes, the knowledge that higher adiposity may prevent fragility fractures has very limited potential for practical application. Today, promoting weight gain to prevent fragility fractures would not be a reasonable population-wide policy given the small comparative burden of bone fragility when compared to the multiple adverse health outcomes that result from obesity. Therefore, whereas we may be reasonably confident of the internal and external validity of those findings, there is a systemic barrier for translation, i.e. this particular piece of knowledge is not likely to be useful in most current social contexts, where preventing obesity is a major public health priority. This illustrates the need to place scientific evidence in its public health context. And in its context, the usefulness of this research is limited, even though its validity may be convincing.

Null findings

There are several other instances in which research has limited translation potential, even if we assume that the results are scientifically sound. The reasons for this are manifold. One of them is null findings. The scientific community is growingly worried about a publication bias which favors the representation of studies where statistical associations are found as opposed to those where there are no “significant” results. To address this, many journals now explicitly state that their decision to publish is independent of the direction and magnitude of associations. Regardless of publication policies, however, unless it disproves an established intervention, the absence of an effect has limited interest for translation into policy. This has certainly been the case in some of our previous studies, where we found no evidence of a specific weight-independent effect of adiposity on bone mass [15], no association between bone turnover markers and bone physical properties in children [22], and no measurable relation between dietary patterns and bone mineral density in adolescents [23]. In practice, those findings are not directly translatable into recommendations for public health policy, regardless of their field-specific value.

Non-modifiable causes and directionality of effects

Another barrier for translation is related to the plausibility or feasibility of interventions. Our previous results showing that early life colic, whose etiology is virtually unknown, can sensitize children to later back pain [24] are probably only mechanistically interesting since no intervention target is presently known. In the same way, our observations that both people with lower socioeconomic position and workers exposed to higher biomechanical demands report musculoskeletal pain more often [25,26], and that women tend to have postural patterns more prone to cause back pain [27] are either impossible to act upon or demand structural changes at the societal level that go far beyond the scope of musculoskeletal health research. There are also instances where human traits are so physiologically linked that it is unrealistic to assume the necessary directionality to pinpoint targets for intervention, as in our previous research showing a close constitutional relation between the development of postural patterns and anthropometry in the first decade of life [28], as well as the associations between psychosocial distress and chronic widespread pain in young adults [29].

Field-specific research

It is also frequent that epidemiologists are interested in questions which may be of practical utility within a narrower community but are less useful as evidence for policy. Our previous work comparing two approaches to quantify the population impact of musculoskeletal disorders suggests that empirical disease clusters are able to capture the high population burden of those conditions on complementary health outcomes while allowing to incorporate multimorbidity from coocurring conditions [30]. This might be a useful consideration for researchers in the field of multimorbidity but it does not seem to have an immediate practical application in terms of health policy. Policy implications are also hard to extract from our work suggesting limited usefulness of peripheral when compared to whole-body densitometry to estimate bone properties in the general pediatric population [31]. This work might be more useful to optimize methods for future etiological studies since the clinical significance of bone densitometry in healthy children is limited. Finally, sometimes the aim is to test conceptual starting points for subsequent mechanistic models, such as in the case of a study where we propose that secular trends of hip fractures across different European countries have shown similar reversals [32], which is a long way from having any practical implications for public health policy.

Replication and significance testing

In the wider epidemiologic community, several other issues related to improving the technical quality of research remain under discussion that are not necessarily compatible with a translation agenda. For instance, the ability to replicate research results is a cornerstone of empirical science with potentially serious implications for policy. Different initiatives have recently called for reforms to improve the reliability of research results [33,34], and failure to replicate may question existing policies. Despite that, successful replication in itself is hardly a game-changer in practice and researchers aiming for translation may tend to invest less effort on the fundamental task of assessing the replicability of previous findings and more on addressing evidence gaps that are likely to have immediate practical application.

The need for practical application may also question another major endeavor, generally very welcomed by epidemiologists, which is abandoning null hypothesis significance testing [35,36]. Whereas dropping dichotomous conclusions based on arbitrary cutoffs is a need that most epidemiologists feel – and it can avoid wrong policy and clinical decisions – it is difficult to imagine a replacement of significance testing likely to be effectively used by decision-makers in the near future, who might feel disengaged in the face of more nuanced evidence. The absence of a dichotomy to assist policy questions that are frequently binary is challenging and may demand revisiting all-or-nothing approaches to research translation. In this scenario, translational epidemiology requires researchers to be equipped with competences to discuss and communicate uncertainty and its implications.

The issue of usefulness

Outside the specific field of epidemiology there have been important theoretical developments on scientific knowledge production and innovation that increasingly stress the interactions between science and society, such as the relatively recent quintuple innovation helix framework, which brings together academic research with industry, government, civil society and the environment [37]. Specifically in the public health domain, several technical frameworks to guide knowledge translation have been developed over the recent years, particularly focusing on evidence dissemination to stakeholders and sustaining the use of evidence in practice [38]. The priority of translation in the research agenda is also clear throughout the research process itself, from funding institutions, who now typically require explicit plans to deliver societal impact, to scientific publications, with journals frequently promoting the statement of practice and/or policy implications of findings - even if sometimes leading researchers to suggest unrealistic or overly generic implications. Also, it seems reasonable to assume that most researchers in epidemiology want their work to influence decision making in the most effective way possible. However, for researchers, judging the potential for research translation seems much more challenging than judging its field-specific value. To some extent, the aim of translating may even raise important questions about the field-specific value of the underlying science. Our work on a national observatory for the rheumatic diseases illustrates some of these issues.

Scientific novelty vs. relevance for policy

In 2010 we examined a large amount of data from a variety of sources, in order to synthesize knowledge on the descriptive epidemiology of rheumatic and musculoskeletal disorders in Portugal, and on the implementation of the national policy for the rheumatic diseases [39]. We reviewed published literature, retrieved baseline information on the frequency of the conditions targeted by the policy, and identified gaps in the knowledge about the burden of inflammatory arthropathies and chronic pain syndromes. In a second step, we monitored the implementation of the strategies defined in the policy. We observed that several structural achievements had been made within the policy time span, including improving the hospital-based provision of care, initiating a national patient register, and producing technical guidelines for specific conditions. Conversely, the strategies that implied multisectoral involvement, namely with professionals outside rheumatology units, were clearly less successful. Importantly, this work also exposed the dissonance between planning of policies and resource allocation. The resulting report was widely disseminated within the rheumatology community in the country, including practitioners and patient advocates, who also contributed to its final version. It was picked up by national media outlets and used as a supporting document for the subsequent National Health Plan 2011–2016 [40]. Throughout the years, it became one of our most cited publications in Portuguese and has served as teaching material in external academic institutions. It seems to have contributed to increase the visibility of rheumatology at the time, and to advocate for the needs of individuals with rheumatic and musculoskeletal conditions. However, if this work were to be assessed through a purely scientific lens, it would probably be considered of low scientific novelty and of limited technical sophistication within the respective research landscape. Despite that, it has probably had more societal impact and a wider reach in Portugal than any other of our other published works. This seems a good example of the frequent divergence between policy-makers' needs and researchers' goals. The main distinctive feature of this project was that since its inception, it was conceived together with different stakeholders who then decided to become users of that knowledge, probably because that was the knowledge they needed at the time. This happened regardless of our own thoughts on the implications of the work, illustrating that the process of translation is not a straightforward or objective one. The way that a set of findings is translated into policy depends on who effectively makes use of those findings and on the context to which they are applied. Ultimately, researchers have limited room for involvement in the final stages of knowledge translation, and aspiring to a “faithful” translation may be narrow-minded and perhaps even arrogant.

Cross-cutting issues on the usefulness of research

The role of epidemiologists in the translation process may be seen as an end-of-grant activity, i.e. how knowledge produced can be fed into existing systems, or built into the entire research process, in an integrative approach that is increasingly promoted [41]. In any case, translation is grounded on specific historical and societal contexts, which can ultimately shape the research agenda towards the production of knowledge that is readily translatable. In order for research to be effectively translated it has to be needed, either explicitly (responding to a known need) or implicitly (exposing an unrecognized need). This raises a number of important issues. The first and arguably the most important is the legitimacy of unneeded research or untranslatable knowledge, which is by no means a new discussion [42]. Scientific research has always been about the pursuit of the unknown, even if we recognize the systemic reality that the knowledge produced by researchers is a result of abilities, training, vision of host institutions, and external funding opportunities, which in turn are shaped by wider social and political contexts. Nevertheless, an overarching pressure towards the production of research that has immediate practical applicability to solve existing problems could be against the very nature of the scientific endeavor, since not all research that ultimately advances scientific knowledge (see e.g. Flexner [42]) may have direct or immediate translation into policy or practice. It should be noted, however, that there is little objectivity in either the technical or the societal judgement of science but it seems clear that they result from different ecosystems. For example, the possibility of translation is framed by historical context, and scientific knowledge may be useless in the short-term but potentially useful down the road, beyond grant horizons or political cycles. Additionally, the science that public health decision-makers need is frequently within the field of implementation research (what works? how should it be delivered?). However, one of the key assumptions of studying implementation is that public health policy is context specific. One can argue that this approach collides to some extent with the universality and reproducibility that shape the identity of science. Also, context-specific research focusing on implementation in particular settings might be less competitive in terms of publication when compared to generalizable outputs that are more readily applicable across different populations. This might be challenging, since publications remain the major technical benchmark for researchers. Understandably, there is no accepted benchmark or metric for research translation or for the quality of the translation process and outputs. Finally, while some scientific knowledge may remain undisputed or “true” across the eras, science as an enterprise is deeply shaped by social and political contexts. Those influences begin in the definition of research agendas and span the whole process of knowledge production up to the translation of findings, in a manner that goes far beyond the strict application of the scientific method. This may be especially relevant in the context of integrative knowledge transfer efforts, where the whole scientific endeavor is co-produced among stakeholders. For researchers, potentially serious ethical issues such as conflicts of interests may arise when research integrates by design stakeholders such as private companies or governing bodies.

Bringing together quality and usefulness

The challenges discussed above illustrate some of the complexity involved in translating epidemiologic research. They show that some research is hardly translatable by design, such as the development of conceptual frameworks or measurement methods, as well as replication or validation studies. And even some research that addresses causal questions may be difficult to translate into practice, namely when it focuses on non-modifiable causes or complex feedback relations, or when its results cannot be acted upon due to null findings or contextual barriers. Those questions, however, remain legitimate research interests and are needed for epidemiological thinking and methods to evolve, and ultimately to better address pragmatic questions. This requires that researchers remain free to answer questions that do not necessarily address contemporary policy or practice questions.

By nature, research questions are more directly translatable when they address specific policy or practice questions. In those cases, an improved focus on the interactions among stakeholders that produce and use research results seems to be a major facilitator of translation. This is patent in a recently-developed framework that puts a major focus on the interconnectedness and feedback among epidemiology, foundational science, and public health stakeholders, in order to improve the process of turning evidence into practice. [43] The examples below illustrate, from the perspective of an epidemiologist, specific technical approaches that can be promoted by researchers to bring together field-specific quality and usefulness of epidemiologic knowledge.

Causal diagrams and target trials

Within the epidemiology community, causal diagrams are generally used to assist the design of investigations and to plan data analysis, since they clarify structural assumptions, including sources of bias and confounding [44]. Another valuable feature is their ability to assist with the formulation and communication of hypotheses outside the scientific community. Diagrams allow for an open discussion on stakeholders' prior beliefs underlying a certain causal question since they are a transparent representation of causes and effects, disclose directionality as well as potential sources of bias, and clarify strategies to address spurious associations. For instance, confounding is a familiar notion to many stakeholders in the public health domain. Because of that, causal effect estimates are frequently perceived as more robust if they are conditioned on as many other variables as possible. However, field-specific knowledge shows that substantial bias may result from unnecessary adjustment [45], and supports a judicious selection of covariates, which can be more readily illustrated using causal diagrams, both at the study design and data analysis stages. A particular case is when the aim is to measure the determinants of change in a defined clinical or policy outcome, where baseline adjustment, although tempting, may introduce substantial bias [46]. When practitioners and/or policy-makers are involved since the study design phase, causal diagrams are relevant to share decisions among stakeholders, namely on a sufficient set of confounders that should be collected and analyzed, based on agreed assumptions. In our case, they have been particularly useful in the context of collaborative clinical studies, to guide participant selection and to distinguish between interventions that change prognosis, markers of prognosis and confounders [47,48]. For example, we were involved in a case-control study on the effect of serum vitamin D on bone fragility, where cases were patients admitted to the hospital due to incident hip fracture. There was a plan to recruit controls from nursing homes in the same catchment area. In this case, by representing ‘selection for the study’ as a collider in a causal diagram during a stakeholder discussion, we were able to clarify that the recruitment of those controls, who frequently have multimorbidity that leads to vitamin D deficiency, would likely result in an underestimation of vitamin D levels in the target population and introduce substantial selection bias. Another example is related to inflammatory disease monitoring in rheumatology. Disease activity scores are routinely collected as part of regular clinical follow-up in patients with inflammatory arthropathies and it is tempting to include them in quantitative models aiming to assess the effects of modifiable exposures such as diet or pharmacological interventions on disease prognosis. Here, causal diagrams have been particularly useful to clarify that point-in-time disease activity is typically an intermediate step towards harder outcomes (e.g. structural damage, functional limitations or quality of life) rather than a confounder and therefore should not be adjusted for routinely. Finally, in the cases where knowledge users are involved only when the core research process is finished, diagrams can be useful for policy-makers to have better access to the main hypothesis as well as to other causal assumptions on common causes and effects. For example, in a study on the effect of adiposity on adolescent bone, causal diagrams clarified our hypothesis and findings on the weight-independent effect of adiposity on bone density [15], which was considered helpful by external stakeholders to distinguish the effect of mechanical load from that of adiposity.

The target-trial framework is another useful application of the counterfactual model that poses the question “What would be the design of a randomized controlled trial to test this?” [49]. Formulating hypotheses in terms of an experimental design is particularly helpful to show the importance of exposure definition and its practical implications. For instance, when we aimed to quantify the effect of exposure to high work-related biomechanical demands on back pain among young adults, different non-exposed groups (all persons without high demands vs. workers without high demands) implied different causal questions. This could be formulated in terms of a target trial intervention being either 1) working and having high work-related biomechanical demands vs. not working or 2) having high work-related biomechanical demands vs. working and not having high biomechanical demands. This distinction implied substantially different estimates, i.e. most of the observed effect was likely due to working status rather than to specific biomechanical demands, since the magnitude of estimates was considerably larger when exposed workers were compared with non-workers than when comparisons included only workers [26]. Distinguishing between different counterfactuals helped clarify that, if the results are interpreted causally, the expected effect of an intervention to address specific biomechanical exposures among young workers would be much smaller than if the intervention addressed the whole work environment. In terms of translation, this provided a benchmark for the expected outcomes of different preventive approaches, and clarified that planning a focused intervention to decrease biomechanical demands among workers may result in a relatively small benefit when compared to an intervention that addresses whole work environments but requires a more complex multidisciplinary approach.

In our experience, in addition to a fundamental role as part of teaching and training, causal diagrams and target trials can improve the process of translation by improving the quality of inference, as well as the transparency of study design and data analysis. They help counteract obscureness in data-driven approaches while exposing scientific research to external criticism and improving the engagement of practitioners and policy-makers that are most likely to use the resulting evidence.

Modeling of systems

One point epidemiologists, public health practitioners, and policy-makers usually agree on is that population well-being is the result of multiple influences that act and interact at different societal levels to produce a spectrum of health experiences [50]. However, this belief is frequently of little consequence to epidemiologic research, especially since most quantitative models attempt to isolate effects by removing the influence of extraneous intervening factors. In the recent decades, there has been a growing recognition of health systems as complex adaptive systems, which are made up of a large number of heterogeneous elements, and whose behavior adapts over time to changing circumstances and is unpredictable from the knowledge of its individual components alone. Efforts to apply complex systems modeling to public health policy have shown promising results [51]. For example, system dynamics modeling has been used to model structural relations within health systems at higher levels, including the policy level [52]. Qualitative causal loop diagrams are a component of system dynamics modeling that can incorporate group model building strategies and involve partners with knowledge of the system, including public health professionals, policy makers and patients, together with researchers. Such methods are especially interesting to develop realistic approaches to measure the effects of specific policies, i.e. to provide an evidence basis to address specific needs of policy makers, such as assessing the health gains that may result from different interventions. An example where systems modeling could have been decisive in terms of translation is our work on the above-mentioned national policy for the rheumatic diseases. Most of the strategies laid out focused on producing technical guidelines and other instruments to increase the coverage and quality of case finding, and to improve the management of different musculoskeletal conditions. The policy also established several indicators for monitoring and evaluation that were on the most part estimates of the incidence and prevalence of different conditions, such as fragility fractures, osteoarthritis, and back pain. The implicit assumption was that successful implementation would lead to a measurable decrease in the frequency of those conditions. Group model building including the relevant stakeholders at the design stage of the policy would have been useful to reach a common understanding of the implications of different policy scenarios on those indicators. Causal loop diagrams are particularly useful to map out different policies as concurrent and sometimes competing influences on estimated disease burden. For instance, they clarify that several of the proposed policies (e.g. capacitating health professionals for better diagnosis of rheumatic conditions and increasing the coverage of specialized rheumatology centers) are expected to increase the number of incident cases, contributing to an increased inflow (apparent incidence rate) of diagnosed patients into a growing stock of prevalent cases in the target population. They also clarify that improving the long-term management of immune-mediated rheumatic diseases results in a better overall prognosis including lowered mortality, which also contributes to an increasing apparent prevalence due to decreased outflow of patients from the prevalent pool. Those diagrams can also incorporate delays, which are useful to demonstrate that, even in the most optimistic implementation scenarios, desirable outcomes frequently happen beyond the policy's time frame. In this particular case, a system dynamics approach could have been relevant, not to assess the effectiveness of the individual strategies – most of which had a documented evidence base – but to match the interventions planned with adequate monitoring indicators in terms of their sensitivity to change. In practice, it could have clarified that most indicators initially chosen for policy evaluation had limited applicability, both in terms of the extent and direction of change expected within the policy's time horizon. This has been elegantly shown in a diabetes simulation model developed in the US, where the effects of primary prevention measures on avoiding adverse outcomes were stronger but observable much later than those attributable to clinical management policies [52]. Shared structural models of different population-level influences on complex health outcomes can contribute decisively to improve the perceived usefulness of epidemiologic evidence and its translation into public health program evaluation.

Participatory research

The involvement of the civil society in epidemiologic research is increasingly valued, especially of those affected by the conditions being studied, such as patients living with chronic diseases that are complex to manage [53]. Participatory approaches widen the scope of epidemiologic inquiry beyond researcher-initiated questions, and seem particularly promising in the field of rheumatic and musculoskeletal disorders. These conditions are characterized by relatively low case fatality but substantial suffering, worsened by their long duration. The clinical course of rheumatic and musculoskeletal disorders is highly variable, and there is substantial dissociation between clinical disease activity and patient self-assessment of pain, function and general health status [54,55]. In the case of chronic pain, patients frequently recall complex symptom trajectories that are not easily captured in the context of routine clinical assessment, even though they predict long-term prognosis [56], reinforcing that research translation depends on addressing patients' needs in addition to those perceived by policy-makers or practitioners. Patient involvement throughout the research process is essential when aiming to capture the dimensions of chronic pain that are relevant to those affected. To address this, we designed an ongoing study that bridges population-based and clinical cohorts to investigate early markers of adverse musculoskeletal pain trajectories, by bringing together classic clinical symptom attributes with psychophysiological responses to standardized stimuli and long-term explicit memory of pain trajectories [57]. Taking advantage of our previous experience in participatory research in other areas [58], we have designed this study from the outset in collaboration with patient research partners involved in national and international patient associations. This research is still ongoing, and patient research partners have already contributed decisively to formulate study objectives that are of added value to those affected by chronic pain, namely the decision to include a clinical cohort, in addition to advising on how to optimize the process of data collection, and collaborating in the dissemination of the project, within and outside the scientific community. Had we not counted on patient research partners, our approach would have been more limited in terms of the range and nature of outcomes that we are collecting, and probably less likely to be relevant for future translation. In general, participatory research in population-based epidemiology is still in its infancy but it seems particularly well-placed to deliver results that can be translated into policy.

Conclusion

The translation of epidemiologic research raises a number of conceptual, practical and ethical challenges that epidemiologists increasingly need to address. Those include not only the appraisal of field-specific technical quality, which is familiar to researchers, but also judgements on the usefulness and actual use of knowledge, as well as assessments of the legitimacy of research based on translation potential. Several conceptual and technical tools appear promising for guiding future epidemiologic research of consequence. Approaches that formalize the involvement of stakeholders in knowledge production within transparent frameworks open interesting avenues for an effective translation of epidemiologic research projected into the future.

Funding

Research that led to this paper was funded by the European Regional Development Fund (ERDF), through COMPETE 2020 Operational Programme ‘Competitiveness and Internationalization’ together with national funding from the Foundation for Science and Technology (FCT) - Portuguese Ministry of Science, Technology and Higher Education - through the project “STEPACHE - The pediatric roots of amplified pain: from contextual influences to risk stratification” (POCI-01-0145-FEDER-029087, PTDC/SAU-EPI/29087/2017) and by the Epidemiology Research Unit - Instituto de Saúde Pública, Universidade do Porto (EPIUnit) (POCI-01-0145-FEDER-006862; UID/DTP/04750/2019), Administração Regional de Saúde Norte (Regional Department of the Portuguese Ministry of Health) and Calouste Gulbenkian Foundation. This work was also supported by a research grant from FOREUM Foundation for Research in Rheumatology (Career Research Grant).

Declaration of Competing Interest

The authors declare that they have no known competing financial interests or personal relationships that could have appeared to influence the work reported in this paper.