Increasingly, there is a need for national governments, public-private partnerships, private sector and other funding agencies to set priorities in health research investments in a fair and transparent way. A process of priority setting is always an activity driven by values of wide range of stakeholders, which are often conflicting. This process always occurs in a highly specific context (eg, agreed policies and targets in terms of disease burden reduction and time limit, defined geographic space, population and specific health problems).
Child Health and Nutrition Research Initiative (CHNRI) held a series of expert meetings during which a list of 20 universal challenges inherent to research prioritization was identified. Based on these challenges, several key concepts were proposed and defined, including the boundaries of health research, its main domains, and possible criteria for prioritization between competing research investment options. If accepted, these concepts could form a basis for a transparent decision-making framework for setting priorities in health research investments.
CHNRI first proposed that “health research” funded by public funds should be regarded as an activity undertaken to generate presently non-existing knowledge that will eventually be used to reduce the existing disease burden (or other health-related problem) in the population that provided funding. Three universal and non-overlapping domains of health research were proposed as follows: 1) research to assess the burden of disease and its determinants; 2) research to improve the performance of the existing capacities to reduce disease burden; and 3) research to develop new capacities to reduce the disease burden (or other problem). The focus on disease burden is aligned with internationally agreed goals, but it can also be changed to address differences in interests of the investors (such as patentable products for private sector, etc). An approach to systematic listing of all competing research avenues, options, and questions is suggested along with a framework for identifying criteria that can discriminate between characteristics of research questions (eg, answerability, ethics, effectiveness, deliverability, affordability, sustainability, maximum potential impact on disease burden, equity, and others).
CHNRI proposes a new approach to undertaking health research priority setting in a fair and transparent way, respecting principles of risk-neutral investing. The process brings together the investors, a group of technical experts, and a larger number of representatives for various other stakeholders. Investors are a part of the process from the outset; they are assisted in defining the context, expected “returns” on the investments, and their risk preferences. The role for technical experts is to systematically list the competing research investment options and to use a set of criteria to discriminate between research options according to their likelihood of reaching the targets. The stakeholders can then weigh different criteria according to their system of values to inform the investors on research priorities.
It is estimated that more than US $130 billion are invested globally into health research each year and the amount has been increasing steadily over the past decade (1). Still, proposals for health research funding are far exceeding the available resources. Increasingly, there is a need to set priorities in health research investments in a fair and legitimate way, using a sound and transparent methodology. In 2005, CHNRI launched a project to develop a systematic methodology for setting priorities in health research investments and to apply it to child health (2). This effort was motivated by a notion that current research investment prioritization approaches suffer from many shortcomings, which may partly be responsible for the persisting high levels of mortality in children globally (3-5). Commission on Health Research for Development stated that “only 5% of global spending on health research in 1986 was devoted to health problems in developing countries, where 93% of the world’s burden of ‘preventable mortality’ occurred” (6). Leroy et al (3) determined the proportion of research on childhood mortality directed toward better medical technology (ie, toward improving old technology or creating new technology) compared with research on technology delivery and utilization. They found that 97% of grants were allocated to developing new technologies, which could reduce child mortality by 22% – a one-third reduction of what could be achieved if the existing technologies were fully utilized (3). Furthermore, in terms of financial support for health systems and policy research, the “10/90 gap” persists and health systems research receives very little funding (7). The World Report on Knowledge for Better Health: Strengthening Health Systems reported similar conclusions (8). All these sources implied that large disproportion existed between the investments in different types of health research, different diseases contributing to overall burden, and between the health needs of the wealthy and the poor.
One of the trends that have been observed is that certain type of research has persistently been awarded funds and, therefore, attracted scientists, while other crucial research, such as child health epidemiology, which many not be as attractive and likely to be funded remained neglected (5,9). Our concern is that the past several decades of rewarding new, attractive, and original ideas, whereby little concern was given to the usefulness of the generated new knowledge for reduction of persisting disease burden in the society, has led to a dramatic increase in the number of basic research studies and growth of impact factors of the journals that publish such research (5). This process inevitably led to an opening of many new and exciting research avenues, but there have been only few examples where the full potential of the new knowledge was realized at the level of public health, ie, used to meet the needs of the community/society. This is particularly unwelcome because the contributions from taxpayers are frequently the main source of funding for health research investments, and it may (to an extent) explain the ongoing lack of progress toward achieving substantial disease burden reduction across the developing world (3). Only recently, these issues have gained more attention (10-12).
The examples above point to the dangers of the status quo, inconsistencies, and imbalances in investing, relative lack of transparency, accountability to high-level goals and strategic directions, difficulties in determining where particular research fits in the process of knowledge translation, and similar issues. Since May 2005, CHNRI organized a series of meetings and workshops that involved more than 100 experts in global child health from different backgrounds. During those meetings, a review of existing principles and practice of research priority setting was undertaken (4) and a strategy of involving all the stakeholders in the process was defined (13). Those two papers were the first in the series of five papers describing the CHNRI methodology that was prepared as a result of the meetings.
The meetings also highlighted a need for defining some universally observed challenges and agreeing on several key concepts that could be helpful in resolving the challenges. A consensus over those concepts would enable systematic, transparent, and rational solutions to the challenges that were identified with respect to research investment priority setting. In this paper, which is the third paper of the series on CHNRI methodology, we exclusively focus on those universal challenges and propose a solution in a form of conceptual framework that should serve to surmount the challenges through the CHNRI priority setting process. Information on the historic approaches, current principles, and practice of priority setting, strategies of involving the stakeholders, specific guidelines for implementing the CHNRI methodology, and its validation and comparison with other similar methodologies can be found in other papers of this series (4,13), and these issues are not a focus of this particular paper.