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Setting priorities in environmental health research

Kogevinas, Manolisa,b,c,d,*


The articles that published in Environmental Epidemiology in September 2017 failed to include the correct publication date.

The publication date for these three articles is September 12, 2017.

The publisher regrets this error.

Environmental Epidemiology. 1(2):e004, December 2017.

doi: 10.1097/EE9.0000000000000001

aISGlobal, Centre for Research in Environmental Epidemiology (CREAL), Barcelona, Spain, bCIBER Epidemiologia y Salud Pública (CIBERESP), Madrid, Spain, cUniversitat Pompeu Fabra (UPF), Barcelona, Spain, dIMIM (Hospital del Mar Medical Research Institute), Barcelona, Spain

Received: 1 August 2017; Accepted 3 August 2017

Published online xxx xxx 2017

Sponsorships or competing interests that may be relevant to content are disclosed at the end of the article.

*Corresponding author. Address: Barcelona Institute for Global Health (ISGlobal), Barcelona Biomedical Research Park (PRBB) (office 194), Doctor Aiguader, 88, 08003 Barcelona, Spain. Tel./fax +34-93 214 7332. E-mail address: (M. Kogevinas).

This is an open-access article distributed under the terms of the Creative Commons Attribution-Non Commercial-No Derivatives License 4.0, where it is permissible to download and share the work provided it is properly cited. The work cannot be changed in any way or used commercially.

In April 2017, WHO-Europe held a workshop to set criteria for priorities in Environmental Health (EH) research aiming to develop the basis for further negotiations and deliberations around a proposed EH research agenda in coming years in Europe. A report from the meeting has become available[1]. As the President of the International Society of Environmental Epidemiology (ISEE), I was invited to participate and present the Society’s views. Although ISEE members are responsible for generating a large part of EH research, as a professional society, ISEE does not formally set research priorities. Thus, what I presented at the WHO workshop and summarize in this paper reflects my own views.

One way to infer research priorities is to see what people are actually working on. In our last conference in Rome in 2016, the dominant themes were air pollution, exposure assessment, climate change/temperature, and child health (Fig. 1). The small number of abstracts on radiation, water, and soil, and also on neurodegenerative diseases, is noteworthy. The relatively few presentations on radiation is, at least to some extent, an artifact arising because this research has traditionally been presented at other conferences. Relatively few presentations on neurodegenerative diseases may reflect the difficulty in studying these diseases, the lack of appropriate funding, or simply that this field has not yet emerged as a high-priority area. On the other hand, a high volume of research does not necessarily mean that a specific area deserves high priority. For example, the WHO workshop highlighted lines of research that are making more marginal contributions and that there is an extensive unnecessary replication of research.

Figure 1

Figure 1

Figure 2 shows the themes 5 years earlier at the ISEE 2011 Barcelona conference that had approximately the same number of participants as the Rome conference. The most striking difference between the 2 conferences is the increase in a number of presentations on the topics of climate change and child health. Tony McMichael in the 1990s was the first ISEE leader to insistently promote research on climate change at our conferences. However, changing research themes takes time, and it is only recently that we have substantial research on the potential health consequences of climate change beyond the direct effects of temperature. The increase in child health research is likely attributable to the broad acceptance of the long-term importance for adult health of early life exposures, combined with an increase in funding for this research globally.

Figure 2

Figure 2

A good starting point is to ask whether guiding bodies such as the WHO or ISEE should actually set EH research priorities. I would argue that there are 2 main reasons to set such priorities: to guide ourselves and to guide funding agencies. Can the community of environmental epidemiologists go along without agreeing on criteria for prioritizing research? We could, but then others will set research priorities for us, and it is probably best if our Society participates and influences this discussion across different fora. We should collectively rethink how we assign funding. Is this a top-down approach imposed from above or should it be bottom-up depending on how we as individual researchers behave? There is no optimal solution, and the European Union (EU) research programs have used different approaches during the last 20 years and are now promoting a mixed system. For many years, the EU experienced the dysfunction of a uniquely top-down approach that ignored research on climate change and on environmental interventions. A solution was not only the promotion of bottom-up approaches such as the European Research Council (ERC) funding program but also better communication with researchers and other stakeholders for taking decisions on top-down priorities.

The WHO workshop was held a few days after the April 2017 Marches for Science that took place in many cities worldwide. This movement was a wake-up call for many of us who had, perhaps, naively assumed that our strong belief in the benefits of science for society was widely shared. I believe that it is widely shared but less universally than what we thought, and there are powerful voices attacking science. There is abundant evidence showing the economic benefits of research. See, for example, the estimated direct benefits from the human genome project from spinoffs, patents, and so on. It has been estimated that investment of 1 US$ in the Human Genome Project produced a return 140 time higher[2]. However, much of the direct benefit from research does not necessarily transfer to the society at large. It should be noted that the biggest part of the economic benefits to society from research is indirect and long term, for example, gains in the society through the creation of employment, wealth, and well-being connected to the development of knowledge and products related to this knowledge. If the triggers for the Marches for Science tell us something, it is that we need to accept that an important part of the research we do, basic or applied, should also be targeted to the direct benefit of society. We should identify societal problems and promote our own capacities to help society through our research and translation efforts. For example, research on climate change should include the development of mitigation and adaptation strategies that will allow cities to avoid the worst effects of climate change on human health. Research on urban health should promote solutions related to transport, including technological solutions that allow individual choices that will help municipal agencies and citizens to improve the quality of life in cities. The importance of developing research that will inform and promote policy, eliminating or mitigating EH problems, cannot be overstated. There is a well-identified disconnect[3] between research (understanding of a problem) and action (policy or other interventions to alleviate the problem). I believe that this gap became evident during the March for Science movement because research often does not address questions or provide evidence in a way that is (immediately) useful for policy or interventions. Of course, even where such evidence exists, there is often failure of society and individuals to appropriately understand and/or act on that evidence. This suggests the need for a continued dialogue between researchers and key stakeholders in a language that both parties understand to enable our research to have maximal impact.

I propose 4 criteria to be used for developing priorities in research:

  • Novelty: Will research in a specific area produce new knowledge? This may include, for example, the identification of the environmental causes of Parkinson’s disease or new research methodologies/approaches such as the exposome, big data, sensors, toxicogenomics, and so on. or the evaluation of causal chains rather than direct exposure–disease relationships.
  • Importance to People: Will the life and well-being of many populations be positively affected? Are there many people exposed? Are exposure levels high? Are exposure levels increasing? Are susceptible populations exposed? Is it a major subclinical effect or a common disease?
  • Impact on Policy: Will research in a specific area produce knowledge that meaningfully informs evidence-based health policies and prevention? This should include evaluation of interventions and issues regarding environmental equity.
  • Technical Innovation and development: Will research produce new technologies and help economic development, for example, through the wide application of sensors or production of new technologies to predict environmental exposure levels or early effects? (A note: the term innovation is also used to define novelty rather than only technological advance as I do here).

These criteria for the evaluation of EH research priorities largely overlap but are not identical with the criteria often used by granting agencies during peer review of specific studies. More importantly, the weight of each of the criteria, for example, novelty, relevance for policy, or technological development, differ when examining a specific study versus a wide area of research. A study may be funded and results published and highly cited because it examines a great novel idea, for example, on environmentally related mechanisms of a disease based on valid methods. Whether this study promotes directly the development of policy or of technological innovation and development is irrelevant. There is abundant evidence that there may be a significant lag between discovery and application as there is abundant evidence on the eventual use of findings from large and innovative studies in the development of patents[4]. When examining, however, the development of research priorities in a wide scientific area such as EH, the criteria used should be wider and cannot focus only on novelty.

The use of these proposed criteria to identify priorities is not straightforward, and application of numerical algorithms to decide on priorities should be avoided. In other areas of research, such as Health Technology Assessment, semiquantitative evaluation systems including an assessment of hierarchy in types of studies (as suggested, for example, in GRADE—Grading of Recommendations, Assessment, Development and Evaluation—that promotes evidence from Randomized Controlled Trials (RCTs)) have been successfully applied[5]. The same system has been erroneously, I believe, proposed for evaluating studies in EH, including regulatory agencies such as the European Food and Safety Authority.

Setting priorities within EH research refers to the development of a priority list of broad research areas (e.g., air pollution vs. climate change vs. child health research) and also setting priorities within these areas. Let us consider an example. Air pollution is the most important environmental exposure worldwide today in terms of the magnitude of health effects measured as Disability-Adjusted Life Years (DALYS) or deaths. So, on the basis of importance, air pollution is without doubt of very high priority. In addition, we already know enough to guide preventive actions. What additional research on air pollution would actually make a difference to policy or reduction of health risks? Do we need more studies characterizing the dose response on mortality? It is always advantageous to refine our estimates, but perhaps this is not what we most need today, at least not in Western Europe or North America. Do we know enough about the potential health benefits of interventions on transportation systems or population approaches to encourage greater adoption of active or public transport? Probably not, and perhaps this research would be judged as higher priority using all 4 criteria.

Thus, the use of the 4 criteria does not lead to clear decisions. In some cases, high priority can be assigned to a specific research area or study because it broadly fulfills all criteria. In other cases, high priority may be assigned as a function of the potential for human harm, even though we may not have strong a priori empirical evidence about this. Wasn’t this the case with health effects of climate change just a few years ago? I doubt that anyone in ISEE (though not persons frequently visiting 26°40′39.86″N 80°02′08.36″W) would have doubts today that climate change was, and is, and will be a high priority area for our research and intervention.

One key lesson from the history of the development of research in Western Europe after the 18th century is that research flourished (in France, Germany, the United Kingdom, later in the United States and more recently in several countries in Asia) when cultures that believed in change and in the importance of technological development also provided the means for doing so. Creative research can certainly be fostered by structured and continuous funding and societal support, although the success of specific researchers and projects to generate groundbreaking findings is mostly unpredictable. By identifying EH research priorities or developing criteria by which to judge such priorities, we do not want to prescribe what science can be done or limit creativity. On the contrary, we want to promote, as best as we can, a research environment that will foster creative research that will have as great an impact on society as possible.

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Conflict of interest statement

The author declares that there is no conflicts of interest with regard to the content of this report.

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I thank Beate Ritz, Michal Krzyzanowski, Sara Adar, Xavier Basagaña, and Josep Maria Antó for comments on my presentation and Greg Wellenius and the members of the ISEE Journal committee for comments on the paper.

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[1]. WHO, Regional Office for EuropeSetting Research Priorities in Environment and Health Report of a Meeting in Cascais, Portugal, 27–28 April 2017Available at: Accessed 16 August 2017.
[2]. Tripp S, Grueber MEconomic Impact of the Human Genome Project. Battelle Technology Partnership Practice2011Available at Accessed 16 August 2017.
[3]. Phoenix C, Osborne NJ, Redshaw C, et alParadigmatic approaches to studying environment and human health: (Forgotten) implications for interdisciplinary research.Environ Sci Policy201325218–8
[4]. Dolgin ENIH research grants yield economic windfall.Nature201754414–15
[5]. Balshem H, Helfand M, Schunemann HJ, et alGRADE guidelines: 3. Rating the quality of evidence.J Clin Epidemiol2011644401–6
Copyright © 2017 The Authors. Published by Wolters Kluwer Health, Inc.