Research Priorities for Airborne Particulate Matter: I. Immediate Priorities and a Long-Range Research Portfolio (1998)

In this chapter, the 10 highest-priority research recommendations, presented in Chapter 4, are integrated and summarized in a ''research investment portfolio" developed by the committee. The analogy to an investment portfolio acknowledges that a research program has multiple goals that change over time, just as an individual financial investor might have a changing overall long-term investment strategy. A financial investment strategy must be responsive to external changes (e.g., changes in income streams, expenses, the stock and bond markets). Similarly, the committee's research investment portfolio relies on continuing responsiveness to new research findings, iterative transfers of knowledge across disciplines, investigative technology, the development of integrated interdisciplinary information, and changes in available resources.

In developing the research portfolio, the committee sought to integrate the scientific value, decisionmaking value, feasibility, sequencing, and rough but informed collective-judgment estimates of the costs of the recommended research activities. Within the portfolio, the 10 recommended research activities are not ranked by relative priority, and the numbers assigned to them are for identification purposes only. The 10 recommendations were judged to be interdependent, and all 10 are highly relevant to the reduction of policy-related uncertainties. All recommendations met the committee's criteria for research selection

(see Chapter 3). The portfolio is designed to maximize growth in critical knowledge as expeditiously and cost effectively as possible through interactive components and iterative stages, providing a continued stream of scientific evidence on a series of hierarchical topics to fill key gaps in the committee's overall research framework.

The committee's portfolio spans a 13-year horizon, from 1998 to 2010, the estimated closure date for scientific input to EPA's anticipated 2012 review of particulate-matter standards. This portfolio, if aggressively and properly implemented by EPA, should result in substantial new information for the next scheduled EPA review of the particulate-matter standards in the year 2002. By that time, critical information would be expected regarding the most biologically important components and characteristics of particulate matter, the toxicological mechanisms through which they act, and how well the data from ambient air monitors represent the actual exposure of people to particulate matter, especially for the most potentially susceptible subpopulations. It is noteworthy that EPA's current timetable (Table 1-1) for the implementation of the new PM_2.5 standards does not envision the implementation of actual control requirements until approximately 2012. The committee believes that the 1998-2010 time span is an interval over which a comprehensive research program could be reasonably anticipated to produce findings that would materially address key uncertainties in a deliberate plan that emphasizes both early and longer-term results. But the pace of research cannot always be adjusted to match the schedule of a regulatory decisionmaking process, which is determined mainly by law, policy, and administrative factors. Some of the committee's recommended research topics (e.g., effects of controlled exposures of susceptible subpopulations to particulate matter) can be quickly and efficiently addressed, with the possibility of definitive findings within a few years. Other research topics (e.g., long-term effects of air pollution on morbidity and mortality) will require substantially more time for resolution. Consequently, there needs to be a commitment to begin some research immediately, to sustain research on the longer-term questions, and to implement and maintain surveillance of the health effects of particulate matter as the new standards are implemented.

The committee's research investment portfolio is summarized in Table 5.1. It is based on the research recommendations presented in Chapter 4. It covers the committee's recommended timing and rough but informed collective-judgment estimates of research costs. The composition of the portfolio changes over time, initially emphasizing exposure assessment and toxicological investigations. Observational and experimental epidemiological studies are mostly deferred until later in the portfolio plan, pending the development of better methods to measure exposure and an enhanced understanding of the health-relevant characteristics of particles.

In Table 5.1, the committee's research plans for human exposure assessment appear first, front-loaded into the early years of the portfolio, because there is an urgent need to characterize actual exposures of potentially susceptible persons to particulate matter and to characterize the biological consequences of those exposures. Methods are already in hand to assess personal exposures to particulate matter and their outcomes, but little investigation has been done or is yet planned by EPA to investigate the particulate-matter exposures of susceptible persons, e.g., those with chronic obstructive pulmonary disease (COPD), asthma, and heart disease. There is also limited information on exposures of children to particulate matter. Further, there is a serious lack of understanding of the relationship of concentrations measured at fixed outdoor monitoring sites with the actual personal exposures of such individuals. Such gaps in knowledge should be addressed immediately in a 3-year program beginning in 1998.

Another phase of exposure assessment research will be needed, beginning in approximately 2001. This component of exposure assessment research should be initiated after the most biologically important constituents and characteristics of particulate matter have been identified through toxicological and clinical studies. Exposures of potentially susceptible subpopulations (as well as the general population) would again be assessed, but this time with emphasis on the components or aspects of particles judged to be most biologically important. At this stage, serious consideration can be given to the strategy of preventive intervention trials and the strategy for use of advanced techniques in new epidemiological studies.

New exposure-assessment tools will be needed, reflecting anticipated

advances in knowledge about particulate-matter toxicity. Monitoring techniques and exposure models will be needed that are specific to those components or attributes of particulate matter that are determined to be most relevant to health (e.g., the metal content or acidity of particles). Monitors will be needed to characterize population exposures, but attention should be mainly directed at monitors and monitoring strategies to provide information beyond that gained from the current practice of placing monitors at fixed outdoor sites. Monitors will also be needed for use in epidemiological studies directed at particles (or their markers) that are found in the initial years of the research portfolio to be linked to toxicity.

The links between particle sources and receptors (i.e., people) need to be characterized more specifically to provide a much better basis for control strategies. Armed with knowledge of the determinants of particle toxicity, the sources of the toxicants need to be identified, and the relationships between sources and exposures must be described. Models to integrate these factors are a priority, because decisionmakers need them for risk management planning.

The committee also recommends (Table 5.1) extensive research on the exposure-dose-response continuum. One immediately addressable gap is the relationship between exposure and dose in persons with underlying lung disease, specifically COPD and asthma. A recent workshop on clinical studies and particulate matter (Utell and Drew 1998) identified candidate particles for clinical studies to include ultrafines, metals, and acid-coated particles, as well as concentrated ambient particles. The committee recommends a 4-year research program to address that gap. In addition, toxicological research efforts need to be directed at particle characteristics determining toxicity, the combined effects of particulate matter and other pollutants, and the toxicological mechanisms involved. The toxicological research recommended by this committee includes in vitro studies, animal studies, and human (clinical) studies. The committee's program initially emphasizes specific characteristics of particles but then shifts its emphasis to the combined effects of exposures to particulate matter with other pollutants. The changing balance reflects the anticipated gains in understanding of the determinants of particulate-matter toxicity in the initial years of the

portfolio, followed by a shift to research on how the most biologically important particles act in combination with other pollutants.

A 6-year program on mechanisms of particle toxicity that significantly increases current efforts is also included. This program would address more fundamental short-term and long-term mechanisms of injury by particles. The research would complement the more descriptive animal and clinical studies on particle characteristics and on the consequences of combined exposures.

The research portfolio also includes epidemiological studies needed to assess the effects of population exposures and to document any biological consequences of changing exposures. In the committee's proposed schedule, funding for major epidemiological studies is deferred until initial planning is accomplished and more information becomes available on exposure measurements for susceptible individuals and the most biologically important aspects of particles. It will be necessary to redirect current research efforts to fill gaps in knowledge of human exposure to ambient particulate matter and copollutants on a timely basis. However, the epidemiological studies can begin as soon as the information on exposures and biologically important particle constituents becomes known. Absent that vital information, epidemiological studies cannot be directly focused on the most relevant pollutants or subpopulations. The principal focus of future epidemiological investigations should be major population-based studies—both observational and intervention trials—directed at gaining an understanding of the health effects of particles, acting alone or in combination with other pollutants, that are found to determine toxicity in mechanistic experimental studies.

Some epidemiological researchers believe that new epidemiological studies should begin immediately. However, this committee, which includes several epidemiologists, concludes that it will be more productive and cost-effective to delay major epidemiological studies until further information on actual human exposure and the most biologically important components or characteristics of particulate matter becomes available. Without such information, the committee does not anticipate that epidemiological studies could be designed to provide much useful information beyond what is already known.

Some scientists have expressed concern that measurement error limits the interpretation of observational epidemiological studies, such as time-series studies and investigations like the Six Cities Study, that address the effects of particulate-matter exposures on individuals. Over the first 3 years in the committee's research portfolio, methodological research using improved exposure data developed in the program will begin to address this persistent concern.

The committee identified the need for support of a number of activities that underpin the development of new methods needed for the recommended research. There is an immediate need for well-characterized animal models of the chronic human diseases associated with susceptibility to particulate matter for future toxicological studies, as well as systems for studies of in vitro exposures to particulate matter and other pollutants. Better epidemiological methods are needed to increase the efficiency of studies of large populations using routinely collected data on health outcomes and air-pollutant concentrations and for using those data for surveillance of the health consequences of implementing air-pollution standards.

The cost estimates for the research portfolio are not based on a formal budgeting process, but drew on the extensive research and research-management experience and collective judgment of the members of this NRC committee (see Appendix A). The committee developed the estimates recognizing that any one research element might turn out to be somewhat more or less costly than estimated, but the overall estimates are based on informed collective judgments of the estimated levels of resources needed to reduce substantially the key uncertainties in regulatory decisionmaking for particulate matter. The committee will refine these estimates as it continues its work in this 5-year NRC study.

The research cost estimates summarized in Table 5.1 are by no means intended to represent the total particulate-matter research budget recommended for EPA or the nation. They reflect only the 10 research activities assigned highest priority by this committee. They do not represent all of the research that needs to be done on particulate matter. Other funding considerations might include the potential waste and undesirability of abruptly terminating lower-priority but

worthwhile and needed research activities that are already under way, the potential difficulty of changing research directions for some of the federal career research scientists in EPA's intramural laboratories, the technical information needs of EPA's regulatory offices, and the infrastructure costs of establishing and maintaining the research centers requested by Congress.

Over time, the research investment portfolio summarized in Table 5.1 would go a long way toward meeting the needs of decisionmakers, providing some answers for the next phase of decisionmaking and others later. The results of this recommended research would fill the key gaps in the committee's framework for establishing links between particulate-matter sources and health risks. Some questions (e.g., the long-term health effects of air pollution on public health) will require sustained investigation.

The research costs estimated by this committee can be viewed as investments in the scientific foundation upon which all particulate-matter regulatory activities of EPA, state and local governments, and the private sector—planning, implementation, monitoring, compliance, and enforcement—will be built. A solid scientific foundation can help ensure that the other investments yield a sound return. An inadequate foundation will lead to continued uncertainty, contentious debates, and potentially unwise investments that fail to minimize the risks of particulate matter to public health.

The committee realizes that questions undoubtedly will remain about some of the key areas of uncertainty, even after new scientific results have been obtained. Therefore, future judgments will need to be made on the adequacy of new scientific information to address those uncertainties and on the appropriateness of moving from one phase of the committee's recommended research strategy to another. Nevertheless, a coherent and effective particulate-matter research program will require a strongly iterative process that assimilates and uses the results of the multidisciplinary research recommended in this report.