The statement of task for this study (Appendix A) called for creation of a prioritized list of flight investigations for the decade 2013-2022. This chapter addresses that request. A prioritized list implies that the elements of the list have been judged and ordered with respect to a set of appropriate criteria. Four criteria were used. The first and most important was science return per dollar invested. Science return was judged with respect to the key science questions described in Chapter 3; costs were estimated via a procedure described below. The second was programmatic balance—striving to achieve an appropriate balance among mission targets across the solar system and an appropriate mix of small, medium, and large missions. The other two criteria were technological readiness and availability of trajectory opportunities within the 2013-2022 time period.
The individual flight projects for the coming decade must be considered within the context of the broader program of planetary exploration. The goal is to develop a fully integrated strategy of flight projects, technology development, and supporting research that maximizes the value of scientific knowledge gained over the decade. All of the recommendations in this chapter are made under the assumption that the following basic programmatic requirements are fully funded:
• Continue missions currently in flight, subject to approval obtained through the appropriate senior review process. These missions include the Cassini mission to the Saturn system, several ongoing Mars missions, the New Horizons mission to Pluto, ongoing Discovery missions, and others. Ensure a level of funding that is adequate for successful operation, analysis of data, and publication of the results of these missions, and for extended missions that afford rich new science return.
• Continue missions currently in development. These include the GRAIL Discovery mission, the Juno New Frontiers mission, and the Mars Science Laboratory (MSL) and MAVEN missions to Mars.
• Increase funding for fundamental research and analysis grant programs, beginning with a 5 percent increase above the total finally approved fiscal year (FY) 2011 expenditures and then growing at an additional 1.5 percent
|Chapter 4 The Primitive Bodies||Chapter 5 The Inner Planets||Chapter 6 Mars||Chapter 7 The Giant Planets||Chapter 8 Satellites|
|Flagship mission||Not proposed; use limited resources to initiate technology program to ensure that cryogenic comet sample return can be carried out in the 2020s.||Top and only priority is the Venus Climate Mission.||Initiate the Mars Sample Return campaign.
First and highest-priority element is Mars Astrobiology Explorer-Cacher.
|Top and only priority for a new flagship mission is the Uranus Orbiter and Probe.
Jupiter Europa Orbiter should:
—Maintain Jupiter system science as high priority
—Designate Jupiter system science as top-ranked priority during approach and early tour phases
—Incorporate Jupiter system science specific needs into jovian tour design.
|Continue Cassini mission.
Highest-priority new missions in priority order:
1. Jupiter Europa Orbiter component of Europa Jupiter System Mission (EJSM)
2. Titan flagship mission
3. Enceladus Orbiter.
|New Frontiers missions||Raise the cost cap.
Goals in priority order:
1. Comet Surface Sample Return
2. Trojan Tour and Rendezvous.
|Regular cadence is highly desirable.
Goals in priority order:
1. Venus In Situ Explorer
2. South Pole-Aitken Basin Sample Return
3. Lunar Geophysical Network.
|Neither Mars Geophysical Network nor Mars Polar Climate missions is recommended at this time.||Current cost cap is insufficient to permit many of the highest-interest missions.
Only possible current mission is Saturn Probe.
|Io Observer is a higher priority than Ganymede Orbiter.|
|Discovery mission||Ensure an appropriate cadence of future Discovery missions.||Ensure a regular cadence of future Discovery missions.||Small spacecraft missions can make important contributions to the study of Mars.||Allow proposals for targeted and facility-class orbital space telescopes in Discovery program.||–|
|International cooperation||–||Continue support via participating scientist programs and Missions of Opportunity.||MSR could proceed as a NASA-only program, but international collaboration is needed to make real progress; Mars Trace Gas Orbiter is an appropriate start.||–||Encourage continued collaboration between NASA, ESA, and JAXA to enable the implementation of all three components of EJSM.|
per year above inflation for the remainder of the decade (Chapter 10). This increase will make it possible to reap the full scientific benefits of ongoing and future flight projects.
• Establish and maintain a significant and steady level of funding (6 to 8 percent of the NASA planetary budget) for development of technologies that will enable future planetary flight projects.
• Continue to support and upgrade the technical expertise and infrastructure in implementing organizations that support solar system exploration missions.
• Continue to convey the results of planetary exploration to the general public via a robust program of education and public outreach.
The 2003 planetary science decadal survey recommended a total of nine missions:1
• The Europa Geophysical Explorer, which was the highest-priority flagship-class mission recommended in the report;
• Five candidate New Frontiers missions—Kuiper Belt-Pluto Explorer, South Pole-Aitken Basin Sample Return, Jupiter Polar Orbiter with Probes, Venus In Situ Explorer, and Comet Surface Sample Return; and
• Three Mars missions—Mars Science Laboratory, Mars Upper Atmosphere Orbiter, and Mars Long-Lived Lander Network.
Mars Sample Return was regarded by the 2003 decadal survey as an important mission for the decade 2013-2022, and technology development for the mission was recommended for the decade covered by that survey. A subsequent National Research Council (NRC) report expanded the list of potential New Frontiers missions to include Network Science, Trojan/Centaur Reconnaissance, Asteroid Rover/Sample Return, Io Observer, and Ganymede Observer.2
Of the missions recommended in the 2003 decadal survey, Kuiper Belt-Pluto Explorer has been implemented with the first New Frontiers mission, New Horizons, launched in 2005. The second New Frontiers mission, Juno, scheduled for launch in 2011, will accomplish most of the goals of the Jupiter Polar Orbiter with Probes mission, albeit without the probes. The MSL has been built and is scheduled for a 2011 launch; as built it is significantly more ambitious and costly than the MSL mission described in the 2003 decadal survey report. The MAVEN Mars Scout mission addresses the objectives of the Mars Upper Atmosphere Orbiter. Missions responsive to the science goals of the South Pole-Aitken Basin Sample Return, the Venus In Situ Explorer, and the Asteroid Rover/Sample Return are now in competition for selection as the third New Frontiers mission.3
For the current decadal survey, only missions that already had a new start (i.e., the president’s budget requested funding for them, the Congress approved this request, and the president signed the budget bill) were assumed a priori to be part of NASA’s plan. All other missions were evaluated on an equal basis to one another. In contrast to the 2003 decadal survey, Mars missions were considered on an equal basis with all other planetary missions.
This decadal survey places considerable emphasis on cost realism. Although NASA has been responsive to the priorities set out in the 2003 decadal survey, the planetary program has been plagued by overly optimistic assumptions about mission costs. Planetary science is not unique in this regard; optimism in the face of technical challenges is common to many costly endeavors.4 Nevertheless, the result has been that far fewer missions have flown than were recommended. Noteworthy examples include the cost growth of the MSL, the periods of reduced tempo of Discovery missions, and the fact that neither of the very high priority missions to orbit Europa and return samples from Mars has yet been initiated. To achieve greater cost realism, this decadal survey has relied heavily on detailed mission studies and cost estimates derived using a methodology specifically designed to quantify technical, schedule, and cost risks inherent in assessing concepts with differing degrees of technical maturity (see Appendix C).
In the course of this decadal survey, the committee commissioned technical studies of many candidate missions (Appendix G) selected for study on the basis of white papers submitted by the scientific community and recommendations made by the survey committee’s five panels. Each study was led by one or more “science advocates” selected by each panel from among its members on the basis of their expertise to represent the panel’s science interests. Conducted by the Jet Propulsion Laboratory, the Applied Physics Laboratory, Goddard Space Flight Center, or Marshall Space Flight Center, the studies were funded by and transmitted to NASA, which then delivered them to the decadal survey committee. Although NASA was aware of the contents of the studies, it was not involved in directing the studies themselves or in their prioritization by the decadal survey.
Using the four prioritization criteria listed above, the committee then selected a subset of the mission for further cost and technical evaluation (CATE) analysis by the Aerospace Corporation, a contractor to the NRC.
The CATE analysis was designed to provide an independent assessment of the technical feasibility of the candidates, as well as to produce a rough estimate of their costs. Because it takes into account many factors when evaluating a mission’s potential costs, including the actual costs of analogous previous missions, the CATE analysis reflects cost impacts that may be beyond the control of project managers and principal investigators.
It includes a probabilistic model of cost growth tied to technical and schedule risks, and hence projects cost growth resulting from insufficient technical maturity identified as part of the technical evaluation. Following NASA policy, costs were estimated at the 70 percent confidence level. Appendix C discusses the CATE analysis in more detail.
The CATE analysis typically returned cost estimates that were significantly higher than the estimates produced by the study teams, primarily because CATE estimates are based on the actual costs of analogous past projects and thus avoid the optimism inherent in other cost estimation processes. Only the independently generated CATE cost estimates were used by the committee in evaluating the candidate missions and in formulating its final recommendations. This intentionally cautious approach was designed to help prevent the unrealistic cost estimates and consequent replanning that have sometimes characterized the planetary program in the past. In the sections below, the committee presents a recommended plan reflecting these conservative cost estimates and also offers recommendations for what could be added to the plan if the estimates prove to be too conservative.
The committee emphasizes that the studies carried out were of specific “point designs” for the mission candidates identified by the committee’s panels. These point designs are a “proof of concept” that such a mission may be feasible, and they provide a basis for developing a cost estimate for the purpose of the decadal survey. The actual missions as flown may differ in their detailed designs and their final costs from what was studied, but in order to maintain a balanced and orderly program, the missions’ final costs must not be allowed to grow significantly beyond those estimated here. This fact is one of many reasons that a cautious approach to cost estimation is appropriate. The sections below also make specific recommendations for steps that should be taken if the projected costs of certain missions grow beyond expected bounds.
The committee’s statement of task divides NASA’s planetary missions into three distinct cost classes: small missions costing less than $450 million current-year dollars, medium missions costing between $450 million and $900 million, and large missions costing more than $900 million current-year dollars. The first cost class corresponds to the Discovery and Mars Scout programs, the second to the New Frontiers program, and the third to the so-called flagship missions. According to the statement of task, it is within the committee’s purview to recommend changes to the classes, including their cost ranges.
As discussed in some detail below, the Discovery program remains vibrant and highly valuable, allowing the science community to propose a diverse range of low-cost missions with short development times and focused science objectives.
The New Frontiers program fills the middle ground between the small and relatively inexpensive Discovery missions and the much larger and more costly flagship missions. Inspired by the success of the Discovery program,
New Frontiers missions are also selected in a competitive process and led by a principal investigator (PI). In contrast to those for the Discovery program, solicitations for New Frontiers are more strategic, restricting proposals to a small number of specific mission goals. New Frontiers missions address focused science goals that cannot be implemented within the Discovery cost cap but that do not require the resources of a flagship mission.
More expensive than the New Frontiers cost cap, flagship missions can cost up to several billion dollars. Strategic in nature and designed to address a wide range of important science objectives at high-priority targets, flagship missions often involve multi-agency and international cooperation. Because of their scientific breadth and high cost they are not PI-led, but they typically carry a large and sophisticated payload of instruments headed in large part by individual PIs. Some also carry so-called facility instruments that typically are provided by the institution that builds the spacecraft. Despite their high costs, flagship missions consistently deliver high science return per dollar invested.
The issue of finding the optimum balance among small, medium, and large missions has been addressed in a recent NRC study.5 The report of a subsequent NRC workshop touched on balance in the context of the decadal survey process: “[The discussion] reinforced the concept of the decadal survey as a strategic package. That is, decadal studies need to provide the best balance of scientific priorities and prioritized missions.”6
The challenge is to assemble a portfolio of missions that achieves a regular tempo of solar system exploration and a level of investigation appropriate for each target object. For example, a program consisting of only flagship missions once per decade may result in long stretches of relatively little new data being generated, leading to a stagnant planetary science community. Conversely, a portfolio of only Discovery-class missions would be incapable of addressing important scientific challenges such as in-depth exploration of the outer planets.
Mission classes are differentiated not only by their costs but also by the timescale of their execution, span of technology, and involvement of the scientific community. Flagship missions like Viking, Galileo, and Cassini ordinarily have a ~10-year development cycle. They require very capable launch vehicles and involve large teams of investigators and a complex of supporting institutions. Each flagship mission is unique in terms of its science objectives and frequently also in terms of the spacecraft used, and so each is often a new development with little use of heritage hardware.
New Frontiers missions, while still complex and challenging, can be executed on timescales of significantly less than a decade. These missions have less extensive, more focused science objectives than do flagship missions and typically take advantage of technological developments from recent prior missions. The institutional arrangements are less complex and the launch vehicle requirements less demanding.
Discovery missions can respond rapidly to new discoveries and changes in scientific priorities. Rapid (~3-year) mission development is feasible, providing opportunities for student participation, rapid infusion and demonstration of technology, and a rapid cadence of missions pursuing science goals. These missions are executable using relatively small launch vehicles.
In studying any given object, there is a natural progression of mission types, from flyby to orbital investigation to in situ exploration to sample return. The missions early in this progression are generally simpler and less costly than the later ones. Because the long-term goals of planetary science involve thorough study of many objects, a balanced portfolio may thus contain a variety of mission categories, depending on the level of investigation conducted previously.
The 2006 NRC report mentioned above developed criteria by which a scientific program might be assessed.7 Although written almost 5 years ago, the criteria, slightly rephrased, are still relevant to the current decadal survey’s goals:
• Capacity to make steady progress—Does the proposed program make reasonable progress toward the science goals set forth in the decadal survey? Are the cadence of missions and the planning process such that new scientific discoveries can be followed up rapidly with new missions, such as small missions in the Discovery program? Does the program smoothly match and complement programs initiated by prior decadal surveys?
• Stability—Can one construct an orderly sequence of missions, meeting overarching science goals, developing advanced technology, nurturing an appropriately sized research and technical community, and providing for appropriate interactions with the international community? Is the program stable under the inevitable budgetary perturbations as well as the occasional mission failures?
• Balance—Is the program structured to contain a mix of small, medium, and large missions that together make the maximum progress toward the science goals envisioned by this decadal survey? Can some of the science objectives be reached or approached with missions of opportunity and by means of piggyback or secondary flights of experiments on other NASA missions?
• Robustness—Is the program robust in that it provides opportunities for the training and development of the next generation of planetary scientists? Is it robust in that it lays the technological foundation for a period longer than the present decade?
The four criteria cited above are not orthogonal. “Balance” in various guises permeates the other three criteria. For example, a balanced portfolio of missions enhances overall program stability; a balanced portfolio of missions provides better assurance of a continuing stream of visible results. A balanced portfolio also helps prevent large fluctuations in demands for workforce and in cost, therefore fitting more easily into the relatively smooth year-to-year NASA budget.
Several factors can upset balance across mission types. Foremost among these are a lack of control and a lack of predictability of mission costs. A 30 percent overrun in the cost of a mission priced at several billion dollars can distort the entire program of planetary science recommended in a given decadal survey.8 Or, as stated in stark language in the NRC report An Assessment of Balance in NASA’s Science Programs, “The major missions in space and Earth science are being executed at costs well in excess of the costs estimated at the time when the missions were recommended in the NRC’s decadal surveys for their disciplines. Consequently, the orderly planning process that has served the space and Earth science communities well has been disrupted, and the balance among large, medium, and small missions has been difficult to maintain.”9 That report continues with the recommendation that NASA should undertake independent, comprehensive and systematic evaluations of the costs to complete each of its space and Earth science missions for the purpose of determining adequacy of budget and schedule.
NASA’s suite of planetary missions for the decade 2013-2022 should consist of a balanced mix of Discovery, New Frontiers, and flagship missions, enabling both a steady stream of new discoveries and the capability to address larger challenges such as sample return missions and outer planet exploration. The program recommended below was designed to achieve an appropriate balance. To prevent the balance among mission classes from becoming skewed, it is crucial that all missions, particularly the most costly ones, be initiated with a good understanding of their probable costs. The CATE process used in this decadal survey was designed specifically to address this issue by taking a realistic approach to cost estimation.
The cost containment record of missions selected through Announcements of Opportunity (AOs) is relatively commendable, with a few notable exceptions of underestimation of mission complexity or other factors. The committee endorses a recent NRC report’s recommendations that NASA undertake the following actions:10
• Ensure that there are adequate levels of project funds for risk reduction and improved cost estimation prior to final selection; and
• Develop a comprehensive, integrated strategy to control cost and schedule growth and enable more frequent science opportunities.
Within the category of small missions are three elements of particular interest: the Discovery program, extended missions for ongoing projects, and Missions of Opportunity.
The Discovery Program
The Discovery program was initiated in 1992 as a way to ensure frequent access to space for planetary science investigations through competed PI-led missions. The low cost and short development times of Discovery missions provide flexibility to address new scientific discoveries on a timescale of significantly less than 10 years. The Discovery program is therefore outside the bounds of a decadal strategic plan, and this decadal survey makes no recommendations for specific Discovery flight missions. The committee stresses, however, that the Discovery program has made important and fundamental contributions to planetary exploration and can continue to do so in the coming decade. The committee gives the Discovery program its strong support.
Chapters 4 through 8 provide examples of the rich array of science that can be addressed with future Discovery missions. At Mercury, orbital missions complementary to MESSENGER could characterize high-latitude, radar-reflective deposits of volatiles, map the mineralogy of the surface, characterize the atmosphere and the magnetosphere, and precisely determine the long-term rotational state. At Venus, platforms including orbiters, balloons, and probes could be used to study the chemistry and dynamics of the lower atmosphere; surface geochemistry and topography; and current and past surface and interior processes. The proximity of the Moon makes it an ideal target for future Discovery missions using both orbital and landed platforms, building on the rich scientific findings of recent lunar missions, and the planned GRAIL and Lunar Atmosphere and Dust Environment Explorer missions.
Potential Discovery missions to Mars include a 1-node geophysical pathfinder station, a polar science orbiter, a dual spacecraft atmosphere-sounding and/or gravity mission, a mission to collect samples of the atmosphere and return them to Earth, a Phobos/Deimos surface exploration mission, and an in situ aerial mission to explore the region of the martian atmosphere not easily accessible from orbit or from the surface. The committee notes that NASA does not intend to continue the Mars Scout program beyond the MAVEN mission, nor does the committee recommend that NASA do otherwise. Instead, the committee recommends that NASA continue to allow proposals for Discovery missions to all planetary bodies, including Mars.
Investigations of primitive bodies are ideally suited for Discovery missions. The vast number and diversity of asteroids and comets provide opportunities to benefit from frequent launches. The proximity of some targets allows missions that can be implemented within the context of the Discovery program. Near the limit of the cost cap, it may be possible to collect and return samples from near-Earth objects (NEOs). The diversity of targets means that proven technologies may be reflown to new targets, reducing mission risk and cost. And the population of scientifically compelling targets is not static, but rather is continually increasing as a consequence of discoveries in the supporting research and analysis programs.
Because there is still so much compelling science that can be addressed by Discovery missions, the committee recommends continuation of the Discovery program at its current level, adjusted for inflation, with a cost cap per mission that is also adjusted for inflation from the current value (i.e., to about $500 million FY2015).
The committee does note that NASA has increased the size and number of external project reviews for Discovery missions to the point that some reviews are counterproductive and disruptive. The committee endorses the recommendation in a recent NRC report that NASA should reassess its approach to external project reviews to ensure that:11
• The value added by each review outweighs the cost (in time and resources) that it places on projects;
• The number and the size of reviews are appropriate given the size of the project; and
• Major reviews, such as preliminary design review and critical design review, occur only when specified success criteria are likely to be met.
Discovery AOs were released in 1994, 1996, 1998, 2000, 2004, 2006, and 2010. The selected missions are listed in Table 9.2. Because Discovery missions are so important for planetary exploration, and so that the community can plan them effectively, the committee recommends a regular, predictable, and preferably rapid (.24-month) cadence for Discovery AO releases and mission selections. Because so many important missions
TABLE 9.2 Discovery Program Mission Selections to Date
|Year of AO||Mission Selected||Launch Date||Description|
|n/a||Near-Earth Asteroid Rendezvous/Shoemaker||February 17,1996||Asteroid orbiter and rendezvous|
|n/a||Near-Earth Asteroid Rendezvous/Shoemaker||February 17, 1996||Asteroid orbiter and rendezvous|
|n/a||Mars Pathfinder||December 4, 1996||Mars lander and Sojourner rover|
|1994||Lunar Prospector||January 6,1998||Lunar orbiter|
|1994||Stardust||February 7,1999||Comet coma sample return|
|1996||Genesis||August 8,2001||Solar wind sample return|
|1996||CONTOUR||July 3, 2002||Flyby of two comet nuclei (lost contact 6 weeks after launch)|
|1998||MESSENGER||August 3, 2004||Mercury orbiter|
|1998||Deep Impact||January 12,2005||Comet impactor and flyby|
|2000||Dawn||September 27, 2007||Orbit of two main-belt asteroids, Vesta and Ceres|
|2000||Kepler||March 6, 2009||Telescope for the detection of extrasolar planets via transit technique|
|2006||GRAIL||Expected 2011||Twin lunar orbiters for gravity mapping|
|2010||To be determineda||To be determined||To be determined|
a On May 5, 2011, following the completion of this report, NASA announced that the candidates for the next Discovery mission are as follows: the [Mars] Geophysical Monitoring Station, Titan Mare Explorer, and the Comet Hopper. A final selection will be made in 2012. Launch is expected in 2016.
can be flown within the current Discovery cost cap (adjusted for inflation), the committee views a steady tempo of Discovery AOs and selections to be more important than increasing the cost cap, as long as launch vehicle costs continue to be excluded.
The committee notes with some concern the increase in time between AO release and mission launch as indicated in Table 9.2. Beginning with Lunar Prospector and continuing through Kepler, the interval from selection to launch for Discovery missions grew steadily from 4 to 9 years. (The expected launch of GRAIL in 2011 would be an exception to this trend.) A hallmark of the Discovery program has been rapid and frequent mission opportunities. The committee urges NASA to assess schedule risks carefully during mission selection, and to plan program budgeting so as to maintain the original goals of the Discovery program.
Additional AO Opportunities
New knowledge regarding solar system objects has come increasingly from a combination of ground- and space-based telescopic platforms. However, there currently is no explicitly defined program in NASA planetary science that provides for proposals for an orbital mission for observation of solar system objects. Although the Discovery program AO issued in 2010 allows missions to “target” any body in the solar system, except the Sun and Earth, it is silent on the meaning of the verb “target.” Based on presentations to the committee’s panels, it appears that a highly capable planetary space telescope in Earth orbit could be accomplished as a Discovery mission. Such a mission could be particularly valuable for observations of the giant planets and their satellites. The committee recommends that future Discovery Announcements of Opportunity allow proposals for space-based telescopes, and that planetary science from space-based telescopes be listed as one of the goals of the Discovery program.
Extended Missions for Ongoing Projects
Mission extensions can be significant and highly productive, and may also enhance missions that undergo changes in scope because of unpredictable events or opportunities. The Cassini and Mars Exploration Rover
extensions are examples of the former, and the “re-purposing” of missions such as Stardust (NExT) and Deep Impact (EPOXI) are examples of the latter. In some cases, particularly the re-purposing of operating spacecraft, fundamentally new science can be enabled. These mission extensions, which require their own funding arrangements, can be treated as independent, small-class missions. The committee supports NASA’s current senior review process for deciding the scientific merits of a proposed mission extension. The committee recommends that early planning be done to provide adequate funding of mission extensions, particularly for flagship missions and missions with international partners.
Missions of Opportunity
Near the end of the past decade, NASA introduced a new acquisition vehicle called Stand Alone Missions of Opportunity (SALMON). This umbrella announcement allows for five different types of Missions of Opportunity:
1. Investigations involving participation in non-NASA space missions through provision of a critical component of the mission, such as a science instrument, technology demonstrations, hardware components, microgravity research experiments, or expertise in critical areas of the mission;
2. Missions with a participating U.S. co-investigator (non-hardware) selected for a science or technology experiment to be built and flown by an agency other than NASA;
3. Investigations that propose a new scientific use of existing NASA spacecraft;
4. Small complete missions that enable realization of science or technology investigations within the specified cost cap; and 5. Focused investigations that address a specific, NASA-identified flight opportunity, a SALMON type under which the U.S.-provided instruments for the 2016 Mars Trace Gas Orbiter were recently acquired.
In addition to their science return, Missions of Opportunity provide a chance for new entrants to join the field, for technologies to be validated, and for future PIs to gain experience. The success of this program will depend on a process that emphasizes flexibility and agility. The committee welcomes the introduction of the highly flexible SALMON approach and recommends that it be used wherever possible to facilitate Mission of Opportunity collaborations.
Mars Trace Gas Orbiter
An important special case of a small mission is the proposed joint European Space Agency (ESA)-NASA Mars Trace Gas Orbiter. A Mars orbiter to study the concentrations, temporal variations, sources, and sinks of atmospheric trace gases, particularly methane, is identified in Chapter 6 of this report as having a high scientific priority. The mission would launch in 2016, with NASA providing the launch vehicle, ESA providing the orbiter, and both agencies providing a joint science payload that was recently selected. Based on the mission’s high value and its relatively low cost to NASA, the committee supports flight of the Mars Trace Gas Orbiter in 2016 as long as the division of responsibilities with ESA outlined above is preserved. Holding to the 2016 launch schedule is important, because failure to do so could significantly affect other missions, particularly to Mars, that are recommended below. As discussed in greater detail below, the Mars Trace Gas Orbiter is intended to be part of a long-term NASA-ESA collaboration on the exploration of Mars.
Optimum Balance Across the Solar System
As described above, NASA’s program of planetary exploration should have an appropriate balance among small, medium, and large missions. It is also important that there be an appropriate balance among the many potential targets in the solar system. Achieving this balance was one of the key factors informing the recommendations
for medium and large missions presented below. The committee notes, however, that there should be no entitlement in a publicly funded program of scientific exploration. Achieving balance must not be used as an excuse for failing to make difficult but necessary choices.
The issues of balance across the solar system and balance among mission sizes are related. For example, it is difficult to investigate targets in the outer solar system with small or even medium missions. Some targets, however, are ideally suited to small missions. The committee’s recommendations below reflect this fact and implicitly assume that Discovery missions will address important questions whose exploration does not require the capacity provided by medium or large missions.
It is not appropriate to achieve balance simply by allocating certain numbers or certain sizes of missions to certain classes of objects. Instead, a scientifically appropriate balance of solar system exploration activities must be found by selecting the set of missions that best addresses the highest priorities among the overarching science questions in Chapter 3. The recommendations below are made in accordance with this principle.
The current New Frontiers cost cap, inflated to FY2015 dollars, is $1.05 billion, including launch vehicle costs. The committee recommends changing the New Frontiers cost cap to $1.0 billion FY2015, excluding launch vehicle costs. This change represents a modest increase in the total cost of a New Frontiers mission provided that the cost of launch vehicles does not rise precipitously; the increase is fully accounted for in the program recommendations below.12 As shown below, this change will allow a scientifically rich and diverse set of New Frontiers missions to be carried out. Importantly, it will also help protect the science content of the New Frontiers program against increases and volatility in launch vehicle costs. Use of technologies like low-thrust propulsion that reduce requirements for launch vehicle performance (and thereby cost) should be given credit in the proposal evaluation process.
High-Priority Medium-Class Mission Candidates
The New Frontiers program to date has resulted in the selection of the New Horizons mission to Pluto (now in flight) and the Juno mission to Jupiter (in development). A competition to select a third New Frontiers mission is now underway, with selection scheduled for 2011.13 In this report the committee addresses subsequent New Frontiers missions, beginning with the fourth, to be selected during the decade 2013-2022.
The committee’s statement of task (Appendix A) calls for a list of specific mission objectives for New missions. On the basis of their science value and projected costs, the committee identified seven candidate New Frontiers missions for the decade 2013-2022. All of these missions address broad and important questions in planetary science and have been judged to have high science merit when considered in light of the community-derived science priorities described in Chapter 3. All are also judged to be plausibly achievable within the recommended New Frontiers cost cap (although, for some, not within the previous cap).14 In alphabetical order, the seven candidate New Frontiers missions recommended by the committee are as follows:
• Comet Surface Sample Return—The objective of this mission is to acquire and return to Earth a macroscopic sample from the surface of a comet nucleus using a sampling technique that preserves organic material in the sample. The mission would also use additional instrumentation on the spacecraft to determine the geologic and geomorphologic context of the sampled region. Because of the increasingly blurred distinction between comets and the most primitive asteroids, many important objectives of an asteroid sample return mission could also be accomplished by this mission.
• Io Observer—The focus of this mission is to determine the internal structure of Io and to investigate the mechanisms that contribute to the satellite’s intense volcanic activity. The spacecraft would go into a highly elliptical orbit around Jupiter, making multiple flybys of Io. Specific science objectives would include characterization of surface geology and heat flow, as well as determination of the composition of erupted materials and study of their interactions with the jovian magnetosphere.
• Lunar Geophysical Network—This mission consists of several identical landers distributed across the lunar surface, each carrying instrumentation for geophysical studies. The primary science objectives of this mission are to characterize the Moon’s internal structure, seismic activity, global heat flow budget, bulk composition, and magnetic field. The mission’s duration would be several years, allowing detailed study of lunar seismic activity and internal structure.
• Lunar South Pole-Aitken Basin Sample Return—The primary science objective of this mission is to return samples from this ancient and deeply excavated impact basin to Earth for characterization and study. In addition to returning at least 1 kg of samples, this mission would also document the geologic context of the landing site with high-resolution and multispectral surface imaging.
• Saturn Probe—This mission is intended to determine the structure of Saturn’s atmosphere as well as abundances of noble gases and isotopic ratios of hydrogen, carbon, nitrogen, and oxygen. The flight system consists of a carrier-relay spacecraft and a probe to be deployed into Saturn’s atmosphere. The probe would make continuous in situ measurements of Saturn’s atmosphere as it descends ~250 km from its initial entry point and relays measurement data to the carrier spacecraft.
• Trojan Tour and Rendezvous—This mission is designed to examine two or more small bodies sharing the orbit of Jupiter, including one or more flybys followed by an extended rendezvous with a Trojan object. Primary science objectives for this mission include characterization of the bulk composition, interior structure, and near-surface volatiles.
• Venus In Situ Explorer—The primary science objectives of this mission are to examine the physics and chemistry of Venus’s atmosphere and crust. This mission would attempt to characterize variables that cannot be measured from orbit, including the detailed composition of the lower atmosphere and the elemental and composition of surface materials. The mission architecture consists of a lander that would acquire atmospheric measurements during descent and then carry out a brief period of remote sensing and in situ measurements on the planet’s surface.
The current competition to select the third New Frontiers mission includes the SAGE mission to Venus and the MoonRise mission to the Moon. These missions are responsive to the science objectives of the Venus In Situ Explorer and the Lunar South Pole-Aitken Basin Sample Return, respectively. The committee assumes that the ongoing NASA evaluation of these two missions has validated their ability to be performed at a cost appropriate for New Frontiers. For the other five listed above, the CATE analyses performed in support of this decadal survey have shown that it may be possible to execute them within the New Frontiers cost cap (see Appendix C).
The committee’s list of recommended New Frontiers mission candidates differs somewhat from that in the most recent NRC report on New Frontiers.15 One mission has been added (Saturn Probe), two have been removed (Asteroid Rover/Sample Return and Ganymede Observer), and one has been narrowed in focus (Network These changes are a result of the committee’s application of the selection criteria listed at the beginning of this chapter, and they reflect changes in scientific knowledge and programmatic realities since the time of the 2008 report.
Decision Rules To achieve an appropriate balance among small, medium, and large missions, NASA should select two New Frontiers missions in the decade 2013-2022. These are referred to below as New Frontiers Mission 4 and New Frontiers Mission 5.
Because preparation and evaluation of New Frontiers proposals places a substantial burden on the community and NASA, it is important to restrict each New Frontiers solicitation to a manageable number of candidate missions. New Frontiers Mission 4 should be selected from among the following five candidates:
• Comet Surface Sample Return,
• Lunar South Pole-Aitken Basin Sample Return,
• Saturn Probe,
• Trojan Tour and Rendezvous, and
• Venus In Situ Explorer.
These five were selected from the seven listed above based on the criteria described at the beginning of this chapter: science return per dollar, programmatic balance, technological readiness, and availability of spacecraft trajectories. All offer the potential for exceptional science return per dollar. Together they address a set of high-priority science objectives that is well balanced across the solar system, especially when considered in conjunction with the large missions recommended below. And all are technically mature and have available trajectories. No relative priorities are assigned to these five mission candidates; instead, the selection among them should be made on the basis of competitive peer review.
If either SAGE or MoonRise is selected by NASA in 2011 as the third New Frontiers mission,16 the corresponding mission candidate should be removed from the above list of five, reducing to four the number of candidates from which NASA should make the New Frontiers Mission 4 selection.
For the New Frontiers Mission 5 selection, the Io Observer and the Lunar Geophysical Network should be added to the list of remaining candidate missions, increasing the total number of candidates for that selection to either five or six. Again, no relative priorities are assigned to any of these mission candidates.
High-Priority Large-Class Missions
The decadal survey has identified five candidate flagship missions for the decade 2013-2022. All of these missions have been judged to have exceptional science merit when considered in light of the community-derived science priorities described in Chapter 3. All are correspondingly costly. In alphabetical order, they are as follows:
• Enceladus Orbiter—This mission would investigate that saturnian satellite’s cryovolcanic activity, habitability, internal structure, chemistry, geology, and interaction with the other bodies of the Saturn system. In particular, it would provide extensive characterization of Enceladus’s plumes, first discovered during the Cassini mission. Upon arrival at Saturn, the spacecraft would orbit the planet for ~3.5 years, allowing numerous flybys of several saturnian moons. It would then go into orbit around Enceladus for a baseline 12-month mission there.
• Jupiter Europa Orbiter—This mission is the stand-alone U.S. component of the proposed NASA-ESA Europa Jupiter System Mission (EJSM). The EJSM consists of two independently launched and operated orbiters: the NASA-led Jupiter Europa Orbiter (JEO) and the ESA-led Jupiter Ganymede Orbiter. Specific science objectives for the JEO include characterization of Europa’s ocean and interior, ice shell, chemistry and composition, and the geology of prospective landing sites. The preliminary mission timeline includes a 30-month jovian system tour phase, followed by a 9-month Europa orbital phase. The mission would also make observations of Jupiter itself.
• Mars Astrobiology Explorer-Cacher—This mission, MAX-C, is the first of three components of a joint NASA-ESA Mars Sample Return campaign. The MAX-C rover is responsible for characterizing a landing site selected for high science potential, and for collecting, documenting, and packaging samples for return to Earth. The rover would also be capable of conducting high-priority in situ science on the martian surface. MAX-C is envisioned as being carried out jointly with ESA’s ExoMars rover mission, with a single entry, descent, and landing system delivering both rovers to the same landing site. In evaluating MAX-C’s science return per dollar, the committee considered the science return of the full Mars Sample Return campaign and the costs of the full NASA portion of that campaign.
• Uranus Orbiter and Probe—This mission consists of a spacecraft that would deploy a small probe into the atmosphere to make in situ measurements of noble gas abundances and isotopic ratios for an ice-giant atmosphere. The spacecraft would then enter into orbit, with the primary science objectives being to make remote sensing measurements of the planet’s atmosphere, interior, magnetic field, and rings, as well as multiple flybys of the larger uranian satellites during the multi-year tour. As described in more detail below, Uranus was chosen over Neptune because of issues involving technology readiness and the availability of appropriate spacecraft trajectories.
• Venus Climate Mission—This mission is designed to address science objectives concerning the Venus atmosphere, including carbon dioxide greenhouse effects, dynamics and variability, surface-atmosphere exchange, and origin. The mission architecture includes a carrier spacecraft, a gondola and balloon system, a mini-probe, and two dropsondes. The mini-probe and dropsondes would each have 45-minute science missions as they descend to the surface, and the gondola and balloon system traveling at a ~55-km float altitude would carry out a 21-day science campaign.
The CATE analyses performed for these five candidate flagship missions yielded estimates for the full life-cycle cost of each mission as defined above, including the cost of the launch vehicle, in FY2015 dollars. For missions with international components (EJSM and MAX-C) only the NASA costs are included. The cost estimates are as follows:
• Enceladus Orbiter, $1.9 billion;
• Jupiter Europa Orbiter, $4.7 billion;
• Mars Astrobiology Explorer-Cacher, $3.5 billion;17
• Uranus Orbiter and Probe, $2.7 billion;18 and
• Venus Climate Mission, $2.4 billion.
These costs are substantial, but on the basis of a long history of cost growth for complex planetary missions, the committee believes them to be realistic. Because of the high costs of flagship missions and the associated impact on the rest of the planetary program, the decision rules and cost caps discussed below are particularly important.
Large-Class Mission Decision Rules
The committee devoted considerable attention to the relative priorities of the various large-class mission candidates. In particular, both JEO and the Mars Sample Return campaign (beginning with MAX-C) were found to have exceptional science merit when considered in light of the community-derived science goals described in Chapter 3. Because it was difficult to discriminate between Mars Sample Return and JEO on the basis of their anticipated science return per dollar alone, other factors came into play. Foremost among these was the need to maintain programmatic balance by ensuring that no one mission takes up too large a fraction of the planetary budget at any given time.
Notably, Mars Sample Return is broken into three separate missions that can be spaced out over two or even three decades, reducing the per-year costs and thus making it easier for programmatic balance to be maintained. In contrast, the inherent costs of getting any payload to 5 AU are substantial, and examination of JEO showed that breaking it into several smaller missions would not result in significant costs savings. The costs of JEO therefore must be incurred over a much shorter period of time. Mars Sample Return was thus prioritized above JEO not primarily because of its science merit, but for pragmatic reasons associated with the required spending profiles.
The highest-priority flagship mission for the decade 2013-2022 is MAX-C, which will begin the NASA-ESA Mars Sample Return campaign. However, the cost of MAX-C must be constrained in order to maintain programmatic balance.
The Mars community, in their inputs to the decadal survey, was emphatic in their view that a sample return mission is the logical next step in Mars exploration. MAX-C will also explore a new site and significantly advance understanding of the geologic history and evolution of Mars, even before the cached samples are returned to Earth. Because of its potential to address essential questions regarding planetary habitability and life, Mars sample return has been a primary goal for Mars exploration for many years. It directly addresses all three of the crosscutting science themes of Chapter 3, and it is central to the theme of planetary habitability. Mars science has reached a level of sophistication such that fundamental advances in addressing the important questions in Chapter 3 will come only from analysis of returned samples.
Unfortunately, at an independently estimated cost of $3.5 billion, MAX-C would take up a disproportionate near-term share of the overall budget for NASA’s Planetary Science Division. This very high cost results in large part from two large and capable rovers—both a NASA sample-caching rover and the ESA’s ExoMars rover—being
jointly delivered by a single entry, descent, and landing (EDL) system derived from the MSL EDL system. The CATE results for MAX-C projected that accommodation of two such large rovers would require major redesign of the MSL EDL system with substantial associated cost growth.
The committee recommends that NASA should fly the MAX-C mission in the decade 2013-2022 only if it can be conducted for a cost to NASA of no more than approximately $2.5 billion (FY2015 dollars). This cost should be verified via an independent CATE analysis conducted after the mission architecture has been defined in adequate detail. If a cost of no more than about $2.5 billion FY2015 cannot be verified, the mission (and the subsequent elements of Mars Sample Return) should be deferred until a subsequent decade or canceled outright. No alternate plan for Mars exploration is recommended by the committee if this were to happen. Sample return is by far the most compelling next step in Mars exploration, and if it cannot be carried out, then the other large-class missions discussed below take precedence over lower-priority Mars missions.
The recommended cost cap of $2.5 billion for MAX-C was arrived at in two ways. The first involved consideration of programmatic balance: $2.5 billion was the highest cost that the committee considered was appropriate for MAX-C without too much of the decadal plan being devoted to Mars exploration. The second was a simple and very conservative cost estimate. The committee asked the Aerospace Corporation to estimate the costs of a worst-case scenario in which the MAX-C mission was flown as currently designed but with the ESA component removed. The estimated cost was just under $2.5 billion. This is not an optimal design for a descoped mission, of course, and it is important to include a significant ESA component within the recommended cap. But these considerations suggest that $2.5 billion for a descoped MAX-C mission is both appropriate and achievable.
It is likely that a significant reduction in mission scope will be needed to keep the cost of MAX-C below $2.5 billion. A key part of this reduction in scope is likely to be reducing landed mass and volume. In particular, it is crucial to preserve, as much as possible, both the system structure and the individual elements of the MSL EDL system, realizing that any changes threaten the tested maturity of this system and may lead to expensive re-verification and/or a significant decrease in capability. A significant reduction in landed mass and volume can be expected to lead to a significant reduction in the scientific capabilities of the vehicles delivered to the surface.
The committee recognizes that MAX-C is envisioned by NASA to be part of a joint NASA-ESA program of Mars exploration that also includes the 2016 Mars Trace Gas Orbiter. To be of benefit to NASA, this partnership must also involve ESA participation in other missions of the three-mission Mars Sample Return campaign. Indeed, NASA is unlikely to be able to afford two more missions to return samples in the following decade unless the partnership continues into that decade and ESA makes significant contributions to the costs of those missions. It is therefore crucial to both parties for the partnership to be preserved. The best way to maintain the partnership will be an equitable reduction in scope of both the NASA and the ESA objectives for the MAX-C/ExoMars mission, so that both parties still benefit from it. The guiding principle for any descope process should be to preserve the highest-priority science objectives of the total Mars program for both agencies while reducing costs to acceptable levels. For NASA in the coming decade, this principle means that MAX-C should acquire adequately characterized samples at a cost of no more than $2.5 billion. And because both the NASA and the ESA elements of the mission will be delivered to the same landing site, it is important to make their descoped science as complementary as possible.
As described below, the two subsequent missions in the Mars Sample Return campaign would take place after 2022. The timing is flexible; as described in Chapter 6, the MAX-C sample cache is designed to remain scientifically viable for at least 20 years. The committee has therefore taken the unusual step of recommending a plan for the coming decade that also has significant budget implications for one or even two decades beyond. The committee does this intentionally and explicitly, with the realization that important multi-decade efforts like Mars Sample Return can come about only if such recommendations are made and followed. As noted above, the committee’s recommendation is predicated on the assumption that collaboration with ESA will be maintained throughout the length of the Mars Sample Return campaign, offsetting some of NASA’s costs. It is also important for the science return from the combined MAX-C/ExoMars mission to be significant even if the samples are never returned. Given the ambitious goals of MAX-C/ExoMars, this should be possible even if major descopes are necessary. The committee also stresses that significant sample-return technology investment in the decade 2013-2022 will be necessary, as discussed in more detail below.
A final point regarding MAX-C is that its success depends in part on the success of the MSL EDL system. If that system functions properly in 2012, then a $2.5 billion MAX-C mission should go forward for launch in 2018. If it fails, however, then NASA will have to reconsider the priority and schedule for MAX-C. If the cause of failure can be determined and appropriate and affordable changes can be made in time to preserve a 2018 launch, then MAX-C can continue on schedule. But if uncertainties remain or if the necessary changes cannot be made by 2018, then MAX-C should slip in priority and schedule relative to other large-class missions.
The second-highest-priority flagship mission for the decade 2013-2022 is Jupiter Europa Orbiter. However, as it is currently designed, JEO has a cost that is so high that both a decrease in mission scope and an increase in NASA’s planetary budget are necessary to make it affordable.
The Europa Geophysical Explorer, from which the JEO concept is derived, was the one flagship mission recommended in the 2003 planetary science decadal survey. The scientific case for this mission was compelling then, and it remains compelling now. There is strong evidence that Europa has an ocean of liquid water beneath its icy crust. Because of this ocean’s potential suitability for life, Europa is one of the most important targets in all of planetary science. As its name implies, JEO will also accomplish other important science in the Jupiter system, including studies of other moons and of the planet itself. Like MAX-C, JEO directly addresses all three of the crosscutting themes of Chapter 3 and is, in particular, central to the theme of planetary habitats. Substantial technology work has been done on JEO over the past decade, with the result that NASA is much more capable of accomplishing this mission than was the case 10 years ago.
The difficulty in achieving JEO is its cost. The projected cost of the mission as currently designed is $4.7 billion FY2015. If JEO were to be funded at this level within the currently projected NASA planetary budget, it would lead to an unacceptable programmatic imbalance, eliminating too many other important missions. Therefore, while the committee recommends JEO as the second-highest-priority flagship mission, close behind MAX-C, JEO should fly in the decade 2013-2022 only if changes to both the mission and the NASA planetary budget make it affordable without eliminating any other recommended missions. These changes are likely to involve both a reduction in mission scope and a formal budgetary new start for JEO that is accompanied by an increase in the NASA planetary budget.
It is clearly crucial to keep as small as possible the budget increase required to enable JEO. Because of the maturity of the current JEO mission concept, the committee did not attempt to redesign the mission for lower cost. However, such a redesign is essential for this important mission to be viable. Possible pathways to lower cost include use of a larger launch vehicle that would reduce cost risk by shortening and simplifying the mission design, and a significant reduction in the science payload. Other possible descopes were listed in section 4.1.5 of the 2008 JEO mission study final report.19NASA should immediately undertake an effort to find major cost reductions for JEO, with the goal of minimizing the size of the budget increase necessary to enable the mission. As noted below, the committee also recommends that JEO switch to Advanced Stirling Radioisotope Generators for power production, rather than using Multi-Mission Radioisotope Thermoelectric Generators, to reduce the amount of plutonium-238 necessary to carry out the mission.
The third-highest-priority flagship mission is the Uranus Orbiter and Probe mission. Galileo, Cassini, and Juno have performed or will perform spectacular in-depth investigations of Jupiter and Saturn. The Kepler mission and microlensing surveys have shown that many exoplanets are ice-giant size. Exploration of the ice giants Uranus and Neptune is therefore the obvious and important next step in the exploration of the giant planets. A mission to one of these planets addresses all three of the crosscutting themes in Chapter 3. These planets are fundamentally different from Jupiter and Saturn, and a comprehensive mission to study one of them offers enormous potential for new discoveries.
The committee carefully investigated missions to both Uranus and Neptune. Although both missions have high scientific merit, the conclusion was that a Uranus mission is favored for the decade 2013-2022 for practical reasons. These reasons include the lack of optimal trajectories to Neptune in that time period, long flight times incompatible with the use of Advanced Stirling Radioisotope Generators for spacecraft power, the risks associated with aerocapture at Neptune, and the high cost of delivery to Neptune. Because of its outstanding scientific potential and a projected cost that is well matched to its anticipated science return, the Uranus Orbiter and Probe mission should be initiated in the decade 2013-2022 even if both MAX-C and JEO take place. But
like those other two missions, the Uranus Orbiter and Probe mission should be subjected to rigorous independent cost verification throughout its development and should be descoped or canceled if costs grow significantly above the projected $2.7 billion FY2015.
The fourth- and fifth-highest-priority flagship missions are, in alphabetical order, the Enceladus Orbiter and the Venus Climate Mission. The scientific cases for these missions are presented in Chapters 8 and 5, respectively. To maintain an appropriate balance among small, medium, and large missions, the Enceladus Orbiter and the Venus Climate Mission should be considered for the decade 2013-2022 only if higher-priority flagship missions cannot be flown for unanticipated reasons, or if additional funding makes them possible, as noted below. No relative priority is assigned to these two missions; rather, any choice between them should be made on the basis of programmatic balance. In particular, because of the broad similarity of its science goals to those of JEO, NASA should consider flying the Enceladus Orbiter in the decade 2013-2022 only if JEO is not carried out in that decade.
As emphasized several times, the costs of the recommended flagship missions must not be allowed to grow above the values quoted in this report. Central to accomplishing this cost containment is avoiding “requirements creep”—i.e., the increase in the scope of a mission that sometimes occurs early in its development. The CATE process that was used to estimate mission costs accounts for unanticipated technical problems, but it does not account for a lack of discipline that allows a mission to become too ambitious. To preserve programmatic balance, then, the scope of each of the recommended flagship missions cannot be permitted to increase significantly beyond what was assumed during the committee’s cost estimation process.
EXAMPLE FLIGHT PROGRAMS FOR THE DECADE 2013-2022
Following the priorities and decision rules outlined above, two example programs of solar system exploration can be described for the decade 2013-2022 (Table 9.3). These example programs address the highest-priority questions identified by the planetary science community, and their cost realism is based on CATE analyses conducted in support of the decadal survey. Both assume continued support of all ongoing flight projects, a research and analysis grant program with a 5 percent increase and further growth at 1.5 percent per year above inflation, and $100 million FY2015 annually for technology development.
The recommended program can be conducted assuming a budget increase sufficient to allow a new start for JEO. The cost-constrained program can be conducted assuming the currently projected NASA planetary budget (see Appendix E). The recommended program captures the highest priorities of the planetary science community, but because it does not meet the test of current affordability, the cost-constrained program is also put forward. Notional funding profiles for the two programs are shown in Figure 9.1. The recommended program shown assumes
TABLE 9.3 Two Alternative Flight Programs for the Decade 2013-2022
|Recommended Program||Cost-Constrained Program|
|Discovery program funded at the current level adjusted fo nflation||Discovery program funded at the current level adjusted fo nflation|
|Mars Trace Gas Orbiter conducted jointly with ESA||Mars Trace Gas Orbiter conducted jointly with ESA|
|New Frontiers Mission 4||New Frontiers Mission 4|
|New Frontiers Mission 5||New Frontiers Mission 5|
|MAX-C at $2.5 billion||MAX-C at $2.5 billion|
|Jupiter Europa Orbiter descoped||Uranus Orbiter and Probe|
|Uranus Orbiter and Probe|
NOTE: The recommended program can be conducted assuming an increase in the NASA budget that allows a new start for the Jupiter Europa Orbiter. The cost-constrained program can be conducted within the currently projected NASA Planetary Science Division budget. The ordering of items does not imply priority.
the full $4.7 billion projected for JEO, but the committee emphasizes that this cost can and should be reduced significantly through reductions in mission scope.
FIGURE 9.1 shows that a scientifically rich program can be carried out for the funds expected to be available in the decade 2013-2022, and that a scientifically exceptional program can be carried out with a much-needed budget augmentation. Table 9.4 shows how the recommended program is tied to the three crosscutting themes identified in Chapter 3. The costs projected in Figure 9.1 (bottom) exceed projected funding in some years and fall below it in others, and the year-to-year budget tuning necessary to fit a profile precisely is best left to NASA managers.
As noted, the recommended and cost-constrained programs make realistic assumptions about mission costs, based on the CATE analyses conducted in support of this decadal survey. Plausible circumstances could improve the picture presented above. For example, if the mission costs presented above are overestimates, the budget increase required for the recommended program would be correspondingly smaller. Increased funding for planetary
TABLE 9.4 Crosscutting Science Themes, Key Questions, and the Missions in the Recommended Plan That Address Them
|Crosscutting Theme||Priority Questions||Missions|
|Building new worlds||1. What were the initial stages, conditions, and processe f solar system formation and the nature of the interstella atter that was incorporated?||Comet Surface Sample Return, Trojan Tou nd Rendezvous, Discovery missions|
|2. How did the giant planets and their satellite system ccrete, and is there evidence that they migrated to ne rbital positions?||Jupiter Europa Orbiter, Uranus Orbiter and Probe, Trojan Tour and Rendezvous, Io Observer, Saturn Probe, Enceladus Orbiter|
|3. What governed the accretion, supply of water, chemistry, and internal differentiation of the inner planets an he evolution of their atmospheres, and what roles di ombardment by large projectiles play?||Mars Sample Return, Venus In Situ Explorer, Lunar Geophysical Network, Lunar South Pole-Aitken Basin Sample Return, Trojan Tour and Rendezvous, Comet Surface Sample Return, Venus Climate Mission, Discovery missions|
|Planetary habitats||4. What were the primordial sources of organic matter, an here does organic synthesis continue today?||Mars Sample Return, Jupiter Europa Orbiter, Uranus Orbiter and Probe, Trojan Tour and Rendezvous, Comet Surface Sample Return, Enceladus Orbiter, Discovery missions|
|5. Did Mars or Venus host ancient aqueous environment onducive to early life, and is there evidence that lif merged?||Mars Sample Return, Venus In Situ Explorer, Venus Climate Mission, Discovery missions|
|6. Beyond Earth, are there contemporary habitats elsewher n the solar system with necessary conditions, organi atter, water, energy, and nutrients to sustain life, and d rganisms live there now?||Mars Sample Return, Jupiter Europa Orbiter, Enceladus Orbiter, Discovery missions|
|Workings of sola ystems||7. How do the giant planets serve as laboratories t nderstand Earth, the solar system, and extrasolar planetar ystems?||Jupiter Europa Orbiter, Uranus Orbiter and Probe, Saturn Probe|
|8. What solar system bodies endanger Earth’s biosphere, and what mechanisms shield it?||Comet Surface Sample Return, Discover issions|
|9. Can understanding the roles of physics, chemistry, geology, and dynamics in driving planetary atmosphere nd climates lead to a better understanding of climat hange on Earth?||Mars Sample Return, Jupiter Europa Orbiter, Uranus Orbiter and Probe, Venus In Situ Explorer, Saturn Probe, Venus Climate Mission, Discovery missions|
|10. How have the myriad chemical and physical processe hat shaped the solar system operated, interacted, an volved over time?||All recommended missions|
exploration could make even more missions possible. If funding were increased, the committee’s recommended additions to the plans presented above would be, in priority order:
1. An increase in funding for the Discovery program,
2. Another New Frontiers mission, and
3. Either the Enceladus Orbiter or the Venus Climate Mission.
Not all of the five candidate flagship missions discussed above can be initiated in the decade 2013-2022. The most likely outcome is that three can be initiated if NASA’s planetary budget is augmented, and two if it is not. It is therefore important to look ahead to the following decade and to be fully prepared to consider these missions for flight then. The committee expects that all of the five candidate flagships that are not initiated in 2013-2022 will remain strong candidates at the time of the next decadal survey. Therefore, candidate flagship missions from the list above that cannot be initiated in 2013-2022 should receive thorough technical studies and technology investments, so that they will be ready in time for consideration in the next decade.
It is also possible that the budget picture could turn out to be less favorable than the committee has assumed. This could happen, for example, if the actual budget for solar system exploration is smaller than the projections the committee used. If cuts to the program are necessary, the committee recommends that the first approach should be descoping or delaying flagship missions. Changes to the New Frontiers or Discovery programs should be considered only if adjustments to flagship missions cannot solve the problem. And high priority should be placed on preserving funding for research and analysis programs and for technology development.
The committee identified a number of additional large missions that are of high scientific value but are not recommended for the decade 2013-2022 for a variety of reasons. In alphabetical order, these missions are as follows:
• Ganymede Orbiter—This mission’s primary science objectives are characterization of the satellite’s subsurface ocean, geology, magnetic field, and origin. These objectives would be addressed through three mission phases: a Ganymede flyby phase, a pump-down phase, and an orbital tour phase of 3, 6, or 12 months. Consideration of the Ganymede Orbiter is deferred to the decade following 2013-2022 because of its lower science return per dollar relative to the JEO mission, and because EJSM as currently envisioned would include an ESA-provided spacecraft to study Ganymede, making this mission largely redundant.
• Mars Geophysical Network—The primary science objectives of this mission are to characterize the internal structure, thermal state, and meteorology of Mars. The mission includes two or more identical, independent flight systems, each consisting of a cruise stage, an entry system, and a lander carrying geophysical instrumentation. Science data would be relayed from each lander to an existing orbiting asset to be transmitted back to Earth. Consideration of the Mars Geophysical Network is deferred to the decade following 2013-2022 because of its lower scientific priority relative to the initiation of the Mars Sample Return campaign.
• Mars Sample Return Lander—This, the second component of the Mars Sample Return campaign, consists of a fetch rover to retrieve cached samples on the martian surface and an ascent vehicle to launch the samples into Mars orbit. The MAX-C caching rover will have deposited a small cache container of rock cores on the surface for pickup; the lander would then target a landing ellipse containing the cache and dispatch its fetch rover to retrieve and return the cache to the ascent vehicle. While the fetch process is underway, regolith samples would be collected via a scoop on the lander’s arm; these would also be transferred to the ascent vehicle. The ascent vehicle would then launch the samples into Mars orbit. As noted above, the committee assumes that a significant fraction of the combined cost of this mission and the Mars Sample Return Orbiter (see below) would be borne by the ESA, as part of its partnership with NASA to carry out the Mars Sample Return campaign.
• Mars Sample Return Orbiter—This mission is the third component of the Mars Sample Return campaign. It includes a Mars orbiter, an Earth-entry vehicle, and a terrestrial sample-handling facility. The orbiter is designed to rendezvous with the sample launched into orbit by the Mars Sample Return Lander’s ascent vehicle, and then
transfer this sample into the Earth-entry vehicle and return it to Earth. The Mars Sample Return Lander and the Mars Sample Return Orbiter are deferred to the decade following 2013-2022 because of programmatic balance and the need to execute MAX-C first. Again, the committee assumes that a significant fraction of the combined Mars Sample Return Lander and Orbiter costs would be borne by ESA.
• Neptune System Orbiter and Probe—If unforeseen circumstances were to make it impossible to begin the Uranus Orbiter and Probe mission on the schedule recommended above, Neptune could become an attractive alternate target for most ice-giant system science. The committee’s mission studies indicate, however, that significant hurdles remain in the area of aerocapture or other mission-enabling technologies for a Neptune System Orbiter and Probe to be feasible at a reasonable cost.
• Titan Saturn System Mission—This mission addresses key science questions regarding Saturn’s satellite Titan as well as other bodies in the Saturn system. The baseline mission architecture consists of an orbiter supplied by NASA and a lander and Montgolfière balloon supplied by ESA. These components would examine Titan, concentrating on the prebiotic chemical evolution of the satellite. In addition, in transit to Titan the mission would examine the plumes of Enceladus and take measurements of Saturn’s magnetosphere. As discussed in Chapter 8, consideration of this mission is deferred to the decade following 2013-2022 primarily because of the greater technical readiness of JEO. Its high scientific priority, however, is especially noteworthy. Because the Titan Saturn System Mission is a particularly strong candidate for the future, continued thorough study of it is recommended.
Although consideration of the missions listed above is deferred to the following decade, technology investments must be made in the decade 2013-2022 to enable them and to reduce their costs and risk. In particular, it is important to make significant technology investments in the Mars Sample Return Lander, Mars Sample Return Orbiter, Titan Saturn System Mission, and Neptune System Orbiter and Probe. The first two are necessary to complete the return of samples collected by MAX-C. The Titan Saturn System Mission has the highest priority among the deferred missions to the satellites of the outer planets. Finally, the Neptune System Orbiter and Probe could be an attractive mission for the next decade if the Uranus Orbiter and Probe cannot be flown in the coming decade for some reason. All four missions are technically complex, and so early technology investments are important for reducing cost and risk. The technology needs for these missions are discussed in greater detail in Chapter 11.
The costs of launch services pose a challenge to NASA’s program of planetary exploration. Launch costs have risen in recent years for a variety of reasons, and launch costs today tend to be a larger fraction of total mission costs than they were in the past.
Superimposed on this trend of increasing launch costs are upcoming changes in the fleet of available launch vehicles. The primary launch vehicles likely to be available to support the missions described above are the existing Delta IV and Atlas V families, plus the Taurus II and Falcon 9 vehicles currently under development (Figure 9.2).
Absent from the list of available vehicles is the Delta II rocket that has been so important in launching past planetary missions. The Delta II, whose production has been terminated, proved to be an exceptionally reliable and relatively inexpensive launch vehicle. Although a few Delta II vehicles not assigned to missions remain, the absence of the Delta II will shortly leave a gap in reliable, relatively inexpensive launch capabilities important for missions to the inner planets and some primitive bodies. New vehicles being developed may help to fill this gap. Orbital Sciences Corporation is developing the Taurus II and Minotaur V, while Space Exploration Technology Corporation (SpaceX) is developing the Falcon 9.
As noted, many past missions have relied on the Delta II, and future missions will not have this option. The concern is that alternative launch vehicles of established reliability, such as the Atlas V and the Delta IV, are substantially more expensive even in their smallest versions. The situation is complicated further by the volatility of the costs of these vehicles, and the dependence of costs on future contract negotiations.
Increases in launch costs pose a threat to formulating an effective, balanced planetary exploration program. There may be some ways of partially reducing this threat, although all of them come with their own complexities and disadvantages:
• Use dual manifesting to reduce individual mission costs. Combining two missions with complementary science objectives onto one launch vehicle reduces the costs for each mission. Recent examples of this approach are the Cassini/Huygens mission to Saturn and the Lunar Reconnaissance Orbiter/LCROSS mission to the Moon. This approach, however, does entail additional technical and managerial complications.
• Use dual manifesting for missions to different destinations. For example, a planetary mission could be combined with an Earth observation mission. While significant savings may be possible, such a combination of missions would bring substantial technical and management complications, for example those resulting from the schedule constraints imposed by planetary launch windows.
• Buy blocks of launch vehicles across all NASA users to reduce unit costs. Block procurement of launch vehicles reduces unit costs because of increased production efficiencies both at the prime launch vehicle contractor and at the vendors supplying components and subsystems. According to a 2010 study by the Center for Strategic and International Studies, inefficiency in the U.S. production of launch vehicles adds 30 to 40 percent to U.S. launch costs.20 NASA once procured the Delta II in blocks.
• Buy blocks of launch vehicles across organizations to reduce unit costs. At present, NASA and the Department of Defense procure launch vehicles separately. Combined procurement across both organizations would result
in greater production efficiencies and reduced unit costs. Interagency cooperation to bring about such block buys could be a significant challenge, however.
• Exploit technologies that allow use of smaller, less expensive launch vehicles. For some orbital missions to planets with atmospheres, use of aerocapture can result in a substantial reduction in spacecraft mass, replacing propellants with a less massive heat shield. For other missions, low-thrust in-space propulsion may enable trajectories that have less stringent launch performance requirements. In both instances, of course, launch savings are partially offset by the cost of the necessary technology development.
Radioisotope power systems (RPSs) are necessary for powering spacecraft at large distances from the Sun; in the extreme radiation environment of the inner Galilean satellites; in the low light levels of high martian latitudes, dust storms, and night; for extended operations on the surface of Venus; and during the long lunar night. With some 50 years of technology development, funded by more than $1 billion, and the use of 46 such systems on 26 previous and currently flying spacecraft, the technology, safe handling, and utility of these units are not in doubt.
Although there are more than 3,000 nuclides, few are acceptable for use as radioisotopes in power sources. For robotic spacecraft missions, plutonium-238 stands out as the safest and easiest to procure isotope that is compatible with launch vehicle lift capabilities.
Past NASA use of plutonium-238 in RPSs is well documented. Future requirement planning is subject to periodic (ideally annual) updates to the Department of Energy. Such plans are complicated by cross-agency budgetary expectations, changing NASA plans, and the competitively selected nature of future NASA missions that may require this isotope.
Unfortunately, production of plutonium-238 in the United States ceased in 1988 with the shutdown of the Savannah River Site K-reactor, and separation of the isotope from existing inventories stopped in about 1996. The remaining stock of plutonium-238, largely purchased from Russia, has continued to be drawn down, most recently for the Multi Mission Radioisotope Thermoelectric Generator (MMRTG) on MSL (~3.5 kg of plutonium). An additional potential lien against the remaining supply is the use of plutonium-238 in two Advanced Stirling Radioisotope Generators (ASRGs) on the next Discovery mission (~1.8 kg of plutonium). Although an exact accounting of plutonium-238 in the United States is not publicly available, previous estimates are consistent with a current supply of ~16.8 kg, not including the 3.5 kg now on MSL. Recent NASA requirements reported to DOE are given in Table 9.5.
The projected need decreased from 2008 to 2010 largely due to dropping the lunar rovers associated with the Constellation program (56 kg of plutonium), but also due to a better understanding of requirements. The current plan assumes that an additional 10 kg of plutonium-238 will be purchased from Russia, and that an average of 1.5 kg/yr of new domestic production can begin, but no earlier than 2015. Purchase from Russia is subject to ongoing negotiations, and requests for monies for startup of domestic production were rejected in 2010 by the Congress. Hence, neither of these sources is assured at this time, and without at least 5 kg of new material from Russia as well as renewed U.S. production, NASA’s current plans for future planetary missions cannot be carried out.
This decadal survey recommends a variety of missions and mission candidates (under the New Frontiers program) that require RPSs. As such, these recommendations would modify to some degree NASA’s requirements for plutonium-238. The current supply of plutonium-238 is sufficient to fuel four MMRTGs plus three ASRGs, or 19 ASRGs, or equivalent combinations of the two.
The largest user of plutonium-238 is any mission that has MMRTGs rather than ASRGs as a baseline. Currently this approach applies only to JEO, for which five MMRTGs are baselined—i.e., one more than can be supported by the current supply of plutonium-238. The Titan Saturn System Mission is the only other mission that uses MMRTG as a baseline, and it is deferred until the decade subsequent to this study.
None of the recommended Mars missions use an RPS. Of the potential New Frontiers missions requiring RPSs, Io Observer requires two ASRGs; LGN, four; Saturn Probe, two; and Trojan Tour and Rendezvous, two. Hence, a maximum of six ASRGs for two New Frontiers missions brackets potential requirements. The Uranus Orbiter and Probe and the Enceladus Orbiter each require three ASRGs and cannot be carried out with MMRTGs due to the
TABLE 9.5 Comparison of NASA Requirements for Plutonium-238 as Reported to DOE in 2008 and 2010
|NASA Administrator Letter of April 29, 2008||NASA Administrator Letter of March 25, 2010|
|Mission||Projected Launch||Power (We)||Pu-238 Usage (kg)||Projected Launch||Power (We)||Pu-238 Usage (kg)|
|Mars Science Laboratory||2009||100||3.5||2011||100||3.5|
|Mars (radioisotope power system and heater units)||–a||–a||–a||2018||280||1.8|
|Outer Planets Flagship 1||2017||700-850||24.6||2020||612||21.3|
|New Frontiers 4||2021||800||5.3||2022||280||1.8|
|New Frontiers 5||2026||250-800||1.8-5.3||2027||280||1.8|
|Outer Planets Flagship 2||2027||600-1,000||5.3-6.2||–b||–b||–b|
|Pressurized Rover #1||2022||2,000||14||–c||–c||–c|
|Pressurized Rover #2||2026||2,000||14||–c||–c||–c|
|Pressurized Rover #3||2028||2,000||14||–c||–c||–c|
a Not in plan.
b Deleted from plan.
c Projected Exploration Systems Mission Directorate requirements deleted for human missions.
latter’s prohibitive mass. Discovery 12 is needed to qualify ASRGs, and Discovery 14 and 16 could potentially use these as well—each is currently baselined with two. Hence, 15 ASRGs and 5 MMRTGs are implied by the recommended decadal survey plan presented above; the cost-constrained plan would require only 15 ASRGs.
The recommended program cannot be carried out without new plutonium-238 production or completed deliveries from Russia. The cost-constrained program could be, but only if ASRGs work as currently envisioned and are certified for flight in a timely fashion. Moreover, unless additional plutonium-238 is acquired, there will be only three ASRGs available for the subsequent decade, and so there will not be a Europa mission, a Titan Saturn System Mission, a mission to Neptune, or a long-lived mission to the surface of Venus in future decades. There are no technical alternatives to plutonium-238, and the longer the restart of production is delayed, the more it will cost.
As noted above, the largest projected user of plutonium-238 in the recommended program is JEO. Because the use of MMRTGs on JEO would consume so much of this valuable resource, the committee recommends that JEO use ASRGs for power production. The duration of JEO is compatible with ASRG use, and this change would alleviate (though not solve) the immediate plutonium-238 crisis. In addition, because ASRGs are so broadly important to the future of planetary exploration, the committee recommends that the remaining ASRG development and maturation process receive the same priority and attention as a flight project.
All findings in the recent NRC report on RPSs remain valid.21 With the one exception of NASA issuing annual letters to the DOE defining the future demand for plutonium-238, none of the recommendations of that report have been adopted. A decision to wait for a “better time” to fund activities required to restart domestic plutonium production is just a different way of ending the program, eliminating future science missions whose implementation is dependent on this technology.
The committee is alarmed at the very limited availability of plutonium-238 for planetary exploration. Without a restart of domestic production of plutonium-238, it will be impossible for the United States, or any other country, to conduct certain important types of planetary missions after this decade.
There are three main areas in which collaboration with other parts of NASA could benefit the solar system exploration program. First, as noted above, block buys of launch vehicles across NASA have the potential to lower launch costs significantly. Second, astronomical telescopes, both ground-based and space-based, can be used to observe solar system targets. The Hubble Space Telescope has a long history of successful planetary observations, and this collaboration can be a model for future telescopes such as the James Webb Space Telescope.
A third area of possible intra-agency collaboration is with NASA’s Exploration Systems Mission Directorate (ESMD). NASA’s plans for future human exploration of the solar system currently include ESMD-funded robotic precursor missions to the Moon, Mars, and asteroids. Because their focus is preparing for human exploration, rather than science, these are not substitutes for any of the missions recommended above, nor for Discovery missions. And, although robotic precursor missions present opportunities for collaboration, NASA’s Planetary Science Division should be cautious about imposing mission-defining requirements, as the committee noted in Chapter 2. At the start of mission formulation, ESMD should inform the Science Mission Directorate (SMD) about what mission resources, if any, it is willing to allocate. Then, given a negotiated agreement between ESMD and SMD, NASA should offer opportunities for scientists to propose investigations on such missions by issuing AOs in a manner similar to that for participating on international missions or as was done for Lunar Reconnaissance Orbiter.
Because ESMD robotic precursor missions target planetary bodies, they offer particularly good opportunities for reducing launch costs via co-manifesting.
The greatest potential for interagency collaboration is also launch vehicle block buys and co-manifesting, reducing costs for all partner agencies. It will also be important for NASA to form a strong partnership with the Department of Energy in order to obtain the plutonium-238 needed for upcoming planetary missions.
International collaboration is possible in many forms and offers significant opportunities to strengthen NASA’s solar system exploration program. Missions of Opportunity allow U.S. investigators to participate in missions flown by non-U.S. space agencies and should be pursued vigorously. The science of Discovery and New missions can be enhanced at modest instrument accommodation cost to NASA by including instruments and investigators from other nations. As the capabilities of many potential international partners around the world grow, these opportunities will multiply.
All three of the flagship missions in the recommended program have the potential for substantial international collaboration. EJSM would be done collaboratively with ESA, flying both the NASA Jupiter Europa Orbiter and the ESA Jupiter Ganymede Orbiter. These coordinated missions are a good example of a robust international partnership. There are no complex hardware interfaces between the two major international components. Each mission can stand alone on its own scientific merits, but the two conducted jointly can complement and enhance one another’s science return by making synergistic observations. And each would carry an international payload, making the most capable scientific instruments available to each, regardless of their nation of origin.
MAX-C is envisioned to be an international mission, with both the NASA sample collection rover and the ESA ExoMars rover delivered by a NASA-provided derivative of the MSL EDL system. Moreover, it is intended to be the first element of a three-mission Mars Sample Return campaign, with ESA playing a significant role throughout the entire campaign. Unlike EJSM, the interfaces between NASA and ESA elements of MAX-C (and, perhaps, the follow-on elements as well) are complex, and they will have to be managed with great care. As noted above, a particular concern for MAX-C is that an attempt to accommodate two large and capable rovers as currently imagined would be likely to force a costly redesign of the MSL EDL system. To keep NASA’s costs for MAX-C below the recommended $2.5 billion (FY2015), significant reductions in mission scope, including major reductions in landed mass and volume, are likely to be necessary. So while MAX-C offers an opportunity for international collaboration, that collaboration must be managed carefully.
The Uranus Orbiter and Probe mission has not yet been discussed as an international collaboration, but it offers significant potential. As one example, the instrument payload could be selected internationally, strengthening the science while reducing costs to NASA.
1. National Research Council. 2003. New Frontiers in the Solar System: An Integrated Exploration Strategy. The National Academies Press, Washington, D.C.
2. National Research Council. 2008. Opening New Frontiers in Space: Choices for the Next New Frontiers Announcement of Opportunity. The National Academies Press, Washington, D.C.
3. On May 25, 2011, following the completion of this report, NASA selected the OSIRIS-REx asteroid sample-return spacecraft as the third New Frontiers mission. Launch is scheduled for 2016.
4. For a well-documented case see, for example, Independent Comprehensive Review Panel, James Webb Space Telescope (JWST) Independent Comprehensive Review Panel (ICRP): Final Report, NASA, Washington, D.C., October 29, 2010, available at http://www.nasa.gov/pdf/499224main_JWST-ICRP_Report-FINAL.pdf.
5. National Research Council. 2006. An Assessment of Balance in NASA’s Science Programs. The National Academies Press, Washington, D.C.
6. National Research Council. 2007. Decadal Science Strategy Surveys: Report of a Workshop. The National Academies Press, Washington, D.C., p. 20.
7. National Research Council. 2006. An Assessment of Balance in NASA’s Science Programs. The National Academies Press, Washington, D.C.
8. For a graphic example of the damage potential of cost growth see, for example, Table 3.1 of National Research Council, Decadal Science Strategy Surveys: Report of a Workshop, The National Academies Press, Washington, D.C., 2007.
9. National Research Council. 2006. An Assessment of Balance in NASA’s Science Programs. The National Academies Press, Washington, D.C., p. 2.
10. National Research Council. 2010. Controlling Cost Growth of NASA Earth and Space Science Missions. The National Academies Press, Washington, D.C.
11. National Research Council. 2010. Controlling Cost Growth of NASA Earth and Space Science Missions. The National Academies Press, Washington, D.C., p. 38.
12. The committee excluded launch vehicle costs because the current uncertainty of those costs foiled any attempt to estimate their likely magnitude over the next decade. See the section “Launch Vehicle Costs” in this chapter.
13. On May 25, 2011, following the completion of this report, NASA selected the OSIRIS-REx asteroid sample-return spacecraft as the third New Frontiers mission. Launch is scheduled for 2016.
14. Note that the CATE costs for these missions presented in Appendix C include launch vehicle costs. While some CATE estimates (minus launch vehicle costs) exceed the recommended $1.0 billion cost cap, all were judged by the committee to be close enough to the cap that a PI and team could adjust their scope so that they could fit within the cap.
15. National Research Council. 2008. Opening New Frontiers in Space: Choices for the Next New Frontiers Announcement of Opportunity. The National Academies Press, Washington, D.C.
16. On May 25, 2011, following the completion of this report, NASA selected the OSIRIS-REx asteroid sample-return spacecraft as the third New Frontiers mission. Launch is scheduled for 2016.
17. This is the cost of MAX-C only, not the cost of the full Mars Sample Return campaign. Also, the estimate is for the MAX-C mission as currently conceived; in the text below, the committee recommends reductions in scope to keep the cost below $2.5 billion FY2015.
18. This is the version without a solar-electric propulsion stage.
19. NASA and the European Space Agency. 2009. Jupiter Europa Orbiter Mission Study 2008: Final Report. European Space Agency, Paris, France, January 30, 2009. Available at http://sci.esa.int/science-e/www/object/index.cfm?fobjectid=48278.
20. G. Ben Ari, B. Green, J. Hartman, G. Powell, and S. Sanok. 2010. National Security and the Commercial Space Sector: An Analysis and Evaluation of Options for Improving Commercial Access to Space. Center for Strategic and International Studies, Washington, D.C. July. Available at http://csis.org/publication/national-security-and-commercial-space-sector.
21. National Research Council. 2010. Radioisotope Power Systems: An Imperative for Maintaining U.S. Leadership in Space Exploration. The National Academies Press, Washington, D.C.