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Setting Priorities for Space Research: Opportunities and Imperatives (Chapter 4)
Setting Priorities for Space Research
Opportunities and Imperatives
4
The Rationale for Setting Priorities
Priorities reflect ambitions and values. Individuals or organizations set
priorities to ensure that attention is concentrated on the most important
objectives, to ensure that the most important things are done first. To set
priorities effectively, we need to clarify our objectives. We must be confident that
our purpose and operating principles advance, rather than impede, the
achievement of those objectives.
Long-range priorities -should facilitate management of the scientific
research enterprise in a variety of ways. They should indicate directions in which
the program may evolve and stimulate technological development, organizational
evolution, and cooperative arrangements with other agencies and other nations.
There is increasing interest in establishing priorities for federally funded research.
In a study requested by the House Committee on Science, Space, and
REPORT MENU Technology, the Office of Technology Assessment cited three problems with
NOTICE current federal priority setting:1
MEMBERSHIP
PREFACE
First, criteria used in selecting various areas of research and
SUMMARY
megaprojects are not made explicit . . . . Second, there is currently
CHAPTER 1
no mechanism for evaluating the total research portfolio of the
CHAPTER 2
Federal Government in terms of progress toward national
CHAPTER 3
objectives. . . . Third, although scientific merit and mission
CHAPTER 4
relevance must always be the chief criteria used to judge . . . ,
CHAPTER 5
they cannot always be the sole criteria.
Attempts to set priorities in scientific research should concentrate on
specific initiatives or proposals for activities at the margins of ongoing efforts. Just
as it is impossible to say whether painting or music is the more important activity,
it is impossible to rank the disciplines of science or space research in a priority
order. It is essential to concentrate on the initiatives produced by disciplines, not
the disciplines themselves.2
Priorities are necessary at several levels within the national scientific
enterprise and within the space program and scientific research in space
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Setting Priorities for Space Research: Opportunities and Imperatives (Chapter 4)
because science has created a wealth of opportunities for new initiatives. Some
initiatives will contribute more to scientific understanding than others, some will
contribute more to national economic and technological vitality, some will
advance important applications of information from space, and some will assist in
resolving important policy issues. Because we cannot do them all, both science
and the nation need an orderly process leading to the necessary choices.
First, resources will be allocated between scientific efforts and other
compelling national needs. Next, resources will be divided between basic and
applied science and technological development, between scientific research in
space and other ways of obtaining new knowledge. Finally, within space research
itself there is competition for resources between new initiatives and maintenance
of the intellectual and physical infrastructure, as well as competition among the
initiatives themselves.
MOTIVATIONS FOR RECOMMENDING PRIORITIES
There are strong motivations on three levels for creating a scientific
agenda through the establishment of priorities among competing endeavors:
on the national level, to ensure that national goals are served as
effectively as possible;
for all of science, to ensure that a share of available resources
commensurate with benefits is provided; and
within science, to ensure that the most worthwhile scientific endeavors
are given precedence.
There are two principal arguments in favor of acting on these motivations
to achieve consensus and recommend priorities:
Consensus is politically compelling. Scientists, in space research
and other endeavors, believe that the benefits from science justify a share of
resources adequate to pursue the most promising initiatives and to maintain the
vitality of science through support for scientific education and modern scientific
equipment. They also believe that public and political identification of
technological initiatives as "science" may not be in the best interests of science or
in the long-term national interest. Nevertheless, scientists, as individuals or in
groups, have generally restricted their advocacy statements to the disciplines or
initiatives in which they are most interested rather than arguing for a focused
scientific agenda. But an agenda for science or for space research created and
supported by the scientific community should be compelling. If scientists
demonstrate that their agenda responds to national needs and to scientific
imperatives, then they may argue effectively for an adequate share of resources
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Setting Priorities for Space Research: Opportunities and Imperatives (Chapter 4)
and for an orderly progression through the suite of initiatives endorsed by the
community.
If the players will not act, then the spectators will take the stage.3
Because the costs to pursue all opportunities in science or in space research
exceed available resources by a large margin, choices must be made. If
scientists engaged in space research cannot, or will not, set priorities among
opportunities, then others whose own goals may be quite different will take the
stage and make the decisions. Passivity or disarray on the part of the scientists
presents the political process with the opportunity, indeed the necessity, to make
choices, some of which may not be in the best interests of science. None of the
reasons scientists cite for eschewing the strenuous work of reaching a consensus
prevent federal officials or congressional representatives from making the
necessary choices. When others act, it is the scientists who become the
spectators.
COUNTER-ARGUMENTS TO THE COUNTER-ARGUMENTS
A number of arguments against recommending priorities are sometimes
offered by scientists. Some of them are listed below, with explanations as to why
the task group does not find them compelling.
There will be losers. Indeed there will be, but there are losers now.
Certainly, some who enter the priority-setting process will lose; some initiatives
will necessarily be given low priority or cast aside. That happens now, sometimes
for reasons unrelated to the quality of the science. It would seem preferable that
scientists, as a community, help to determine the winners.
The argument over whether to set priorities is a struggle between the
common good and individual goals, between enterprise and risk avoidance, and,
ultimately, between good science and pedestrian endeavors. Consensus in the
scientific community along with effective advocacy will, in all likelihood, produce
more funds and stable funding patterns and hence strengthen science and
increase the opportunities for the recommended initiatives. Some scientists, with
confidence in their programs, will welcome priorities; others, with less compelling
programs, will seek to delay a decision that they suspect will not be in their favor.
Without a process that identifies and promotes good science and strong
initiatives, resources are scattered and the strong subsidize the weak.
Recommending priorities is too difficult, too contentious.
Recommending priorities is difficult and can be accomplished only through a
formal process in which competing initiatives are judged uniformly according to
explicit criteria, preferably on the basis of written material that specifically
addresses the stated criteria. The formality of the process and the existence of
criteria specified in advance both tend to mitigate contention and to diminish the
influence of hidden agendas. Despite the difficulty of setting priorities, all
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Setting Priorities for Space Research: Opportunities and Imperatives (Chapter 4)
scientists do so in their own research programs. In addition, if scientists find it too
difficult to create an agenda for space research, then, as argued above, others
will do it for them.
The community will not be able to maintain consensus. Scientists
loyal to initiatives that do not receive high recommendations may tend to subvert
the process, it is argued, by lobbying policymakers and Congress for special
favor. Such lobbying would tend to undermine the effectiveness of the
consensus. Rather than seeking to restore initiatives that have been abandoned,
losers in the process would be better advised to develop more exciting initiatives.
This argument and the two above combine to make a fourth:
Setting priorities will be counterproductive because the
community will tear itself apart. Moreover, the argument goes, at present, the
rancor of losers is directed at others outside the community; if the community
recommends the priorities, then that rancor will remain within the community and
fester. Of course, there may be some truth to this observation. But such an
outcome can be avoided by insisting on a fair, open, and formal process. Making
decisions demands maturity—both the discipline to follow an agreed-upon,
honest process and the courage to accept unfavorable results; to depend on the
decisions of a bureaucracy is to prolong adolescence. The space research
community should accept responsibility for its own future if it is to be taken
seriously by others.
The low-priority initiatives will not be done. Some argue that
policymakers or the Congress will take advantage of any list of recommended
priorities by eliminating activities with low priorities. But that is precisely the
reason that priorities are recommended—in order that resources can be
concentrated on the highest-priority items. The more sophisticated priority
schemes, such as those discussed below, allow for balance to be achieved by
allocating an appropriate fraction of resources to all essential activities.
Nevertheless, if there are insufficient resources to do everything, it certainly
seems preferable to abandon low-priority initiatives rather than to starve high-
priority ones.
Scientists cannot make political judgments. The crux of this
argument is that once various disciplines put forward scientifically meritorious
proposals, the decisions about relative social benefits and the extent to which the
competing initiatives serve higher national purposes are beyond the purview of
scientists. But the task group believes that in arguing for initiatives, scientists
should be sensitive to national goals and political realities, just as politicians in
considering scientific initiatives should be sensitive to scientific merit. Since
scientists expect support from taxpayers, they should be willing to explain to the
public why some initiatives better serve national purposes.
In a related argument, some scientists assert that only scientific merit
should be considered, that other social benefits are irrelevant or only of minor
concern. This argument is indeed appropriate for basic research. But meaningful
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Setting Priorities for Space Research: Opportunities and Imperatives (Chapter 4)
initiatives, especially in space research, demand a significant fraction of national
resources and thus involve opportunity costs that must be met by reducing other
programs in which social benefits are of prime concern. These questions of social
benefits and programmatic readiness are important to our society, and scientists
must take them into account.
The fact is that scientists do make political judgments about the value of
science and about their initiatives, especially when lobbying for them in agency
councils and before policymakers and Congress. Some scientists also sharply
criticize initiatives that are labeled as science but are approved and pursued for
nonscientific motivations. Since scientists do make political judgments, it would
be advantageous for them to discuss the broader values of initiatives among
themselves and, in presenting their priority recommendations, to illuminate the
political considerations that they found compelling.
SCHEMES FOR PRESENTING PRIORITIES
Statements of priorities, except in restricted classes of activities, cannot
be unequivocal. While it is possible to rank three research missions that are
candidates for new start authorization unambiguously, it is not possible to rank all
activities of science or of space research in a single list. Thus any scheme for
presenting priorities must be hierarchical in nature, with certain classes of
activities given a higher priority than others. Moreover, priority schemes should
distinguish classes of activities that actually can be compared.
Broad categories within which separate priority lists can be prepared have
been proposed.4,5 Such categories might include support for basic research and
the scientific infrastructure, followed by the mandatory efforts, grand initiatives,
and incremental efforts that are part of the forward march of science.6 Such
schemes can then be presented as two-dimensional matrices, with the columns
representing categories and containing activities listed by relative priority. The
federal Committee on Earth Sciences has presented such a priority scheme for
research activities for the U.S. Global Change Research Program, specifying the
relative priorities of items in the columns and of the columns themselves.7
In ranking initiatives or incremental activities, a number of variables and
considerations must be taken into account. First, there is the scientific value to
the proposing discipline and to science more generally. Other considerations
include the probability of success, costs and readiness, alternate opportunities to
acquire the knowledge, and benefits to society. Priority schemes must also
account for unique opportunities presented by unusual events. Moreover, they
must provide for balance and flexibility in the space research program. Finally,
any methodology should include an analysis of the sensitivity of the rankings to
variations in relative weighting of the criteria used.
Readiness is often a key issue in evaluating initiatives. For some, the
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requisite technology and infrastructure will exist; for others it will have to be
developed. Thus readiness to do scientific research in space involves a broad
range of programmatic issues, including the availability of sensors and
instruments, an appropriate spacecraft and launch vehicle, adequate plans for
managing data and information, and the existence of a community of scientists
with the talent and commitment to ensure the success of the initiative.
High priority for a future initiative helps to develop readiness. It stimulates
development of the necessary innovative technology and information
management concepts and thus enhances the national technological
infrastructure. High priority encourages scientists to redirect research and
educational programs in ways that will contribute to the initiative.
EXPERIENCE WITH PRIORITIES IN SPACE RESEARCH
NASA's Office of Space Science and Applications (OSSA), in cooperation
with advisory committees, has adopted a structured approach to the assignment
of priorities within the program and among new initiatives. The current OSSA
approach to developing the mission queue derives from recommendations made
in The Crisis in Space and Earth Sciences,8 which set forth a specific procedure
for setting priorities among candidates for approval as new starts.
OSSA now produces an annual strategic plan that has two important
features. First, it divides the program into five components, including ongoing
efforts, major and moderate missions, small missions, utilization of the Space
Station, and research-base enhancements. Second, priorities among these
components are set, in effect, through a series of decision rules for allocating
resources among them. The procedure for selecting new starts in each fiscal year
from among a list of candidates is a formal one based on the recommendations in
the Crisis report referred to above.
The OSSA strategic planning effort appears to be effective. The annual
budget requests for new initiatives are made in the context of a formal five-year
plan. Clarifying components of the program and specifically setting priorities
among initiatives through creation of a five-year plan for new starts have reduced
uncertainty and divisiveness in the space research community, strengthened
space research, and made the program more attractive to the decision makers
who provide the resources for it.
FOCUSING ON GOALS
In order to set priorities and create an agenda for science or for space
research, we need to determine what is really important, both to science and to
the nation. We need to assess our values and formulate clear and compelling
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goals.
In this context, our national goals at the highest level seem fairly clear:
increase our understanding of ourselves and the world around us and contribute
to national strength and the well-being of the citizens. In seeking to serve these
goals through the scientific enterprise or scientific research in space, we should
then consider the relative importance of more specific goals and objectives:
Maintain the strength of the scientific enterprise.
Concentrate on the most scientifically meritorious initiatives.
Focus on producing information about the world around us in order to
stimulate new perceptions, foster creation of knowledge, advance understanding,
and enable appropriate policy action.
Produce benefits for society, including contributions to national
economic and technological vitality, the creation of national pride and sense of
purpose, education and public enlightenment, and international cooperation.
Clarifying the relative importance of such goals and objectives will help us
to decide what we should do. Knowing what importance others in the decision
process assign to them will help create an agenda that policymakers can
embrace with enthusiasm.
PRIORITIES AND THE FUNDAMENTAL ASSUMPTION
Even a program with clear priorities and a definite agenda must operate
under external constraints. It will be enhanced or impeded by large-scale forces
and by assumptions that may or may not be evident. Scientific research in space
is clearly affected by the objectives of the civil space program, whose most basic
aim has been to foster human spaceflight. This report contends that by
concentrating on acquiring and processing information and converting it into
knowledge and understanding, space research and the space program will
advance science and contribute to national vitality. This is a fundamental
assumption on which to base an agenda for national activities in space.
From the perspective of knowledge to be gained, flight to orbit and
beyond is the enabling technology, not a goal in itself. In all likelihood the civil
space program will eventually evolve, as has aviation, from the days in which
every flight was a miracle to a multifaceted transportation system advancing a
variety of human endeavors.
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NOTES
1. Office of Technology Assessment. 1991. "Summary" in Federally
Funded Research: Decisions for a Decade (U.S. Government Printing Office,
Washington, D.C.) p. 139.
2. This point was made in a report by the Space and Earth Sciences
Advisory Committee, The Crisis in Space and Earth Sciences—A Time for a New
Commitment (NASA Advisory Council, 1986).
3. "[Policy] is like a play in many acts, which unfolds inevitably once the
curtain is raised. To declare that the performance will not take place is an
absurdity. The play will go on, either by means of the actors . . . or by means of
the spectators who mount the stage." Klemens von Metternich. 1880. Aus
Metternich's Nachgelassenen Papieren 8: 190.
4. Press, Frank, "The Dilemma of the Golden Age," address to members
of the National Academy of Sciences (April, 1988).
5. Dutton, John A., and Lawson Crowe. 1988. "Setting Priorities Among
Scientific Initiatives," American Scientist 76: 599-603.
6. Dutton and Crowe, "Setting Priorities Among Scientific Initiatives,"
1988.
7. Committee on Earth Sciences. 1990. Our Changing Planet: The FY
1991 Global Change Research Plan, Executive Summary (U.S. Geological
Survey, Reston, Va.), presented as part of the U.S. President's Fiscal Year 1991
Budget.
8. Space and Earth Sciences Advisory Committee, The Crisis in Space
and Earth Sciences—A Time for a New Commitment, 1986.
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