March 2014 

NASA/CR–2014-218178 

CFD Vision 2030 Study: A Path to 

Revolutionary Computational Aerosciences 

Jeffrey Slotnick and Abdollah Khodadoust 

Boeing Research & Technology, Huntington Beach, California 

Juan Alonso 

Stanford University, Stanford, California 

David Darmofal 

Massachusetts Institute of Technology, Cambridge, Massachusetts 

William Gropp 

National Center for Supercomputing Applications, Urbana, Illinois 

Elizabeth Lurie 

Pratt & Whitney, United Technologies Corporation, East Hartford, Connecticut 

Dimitri Mavriplis 

University of Wyoming, Laramie, Wyoming 
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March 2014 

NASA/CR–2014-218178 

CFD Vision 2030 Study: A Path to 

Revolutionary Computational Aerosciences 

Jeffrey Slotnick and Abdollah Khodadoust 

Boeing Research & Technology, Huntington Beach, California 

Juan Alonso 

Stanford University, Stanford, California 

David Darmofal 

Massachusetts Institute of Technology, Cambridge, Massachusetts 

William Gropp 

National Center for Supercomputing Applications, Urbana, Illinois 

Elizabeth Lurie 

Pratt & Whitney, United Technologies Corporation, East Hartford, Connecticut 

Dimitri Mavriplis 

University of Wyoming, Laramie, Wyoming
Available from: 

NASA Center for AeroSpace Information 

7115 Standard Drive 

Hanover, MD 21076-1320 

443-757-5802 

The use of trademarks or names of manufacturers in this report is for accurate reporting and does not constitute an 

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and Space Administration.
i 

Table of Contents 

1 EXECUTIVE SUMMARY .............................................................................................................................. 1

2 INTRODUCTION ............................................................................................................................................ 4

3 VISION OF CFD IN 2030 ................................................................................................................................ 5

4 CURRENT STATE .......................................................................................................................................... 6

5 CFD TECHNOLOGY GAPS AND IMPEDIMENTS ................................................................................... 9

5.1 Effective Utilization of High-Performance Computing (HPC) ..................................................................9

CASE STUDY 1: Current Utilization of HPC at NASA ......................................................................... 10

5.2 Unsteady Turbulent Flow Simulations Including Transition and Separation ........................................... 12

CASE STUDY 2: LES Cost Estimates and 2030 Outlook ...................................................................... 13

5.3 Autonomous and Reliable CFD Simulation ............................................................................................. 15

CASE STUDY 3: Scalable Solver Development ..................................................................................... 16

5.4 Knowledge Extraction and Visualization ................................................................................................. 18

5.5 Multidisciplinary/Multiphysics Simulations and Frameworks ................................................................. 18

6 TECHNOLOGY DEVELOPMENT PLAN ................................................................................................. 20

6.1 Grand Challenge Problems ....................................................................................................................... 20

CASE STUDY 4: Impact of CFD Tool Development on NASA Science and Space Exploration 

Missions ................................................................................................................................................... 21

6.2 Technology Roadmap ............................................................................................................................... 22

7 RECOMMENDATIONS ............................................................................................................................... 27

7.1 Development of a Comprehensive Revolutionary Computational Aerosciences Program ...................... 28

7.2 Programmatic Considerations ................................................................................................................... 30

CASE STUDY 5: Community Verification and Validation Resources ................................................. 32

7.3 Strategic Considerations ........................................................................................................................... 33

CASE STUDY 6: Sponsored Research Institutes .................................................................................... 34

8 CONCLUSIONS ............................................................................................................................................. 37

9 ACKNOWLEDGMENTS .............................................................................................................................. 37

10 REFERENCES ............................................................................................................................................... 37

APPENDIX A. HIGH PERFORMANCE COMPUTING TRENDS AND FORECAST FOR 2030 ............. 45
ii 

List of Figures 

Figure 1. Technology Development Roadmap ........................................................................... . . 23 

Figure 2. Proposed Enhanced Revolutionary Computational Sciences Program .................................................... 29

Figure 3. Proposed New Revolutionary Computational Sciences (RCA) Program Structure ................................. 29

Figure 4. Changing Predictions About Semiconductor Sizes .................................................................................. 45

List of Tables 

Table 1. Estimated Performance for Leadership-class Systems ................................................................................ 49
1 

1 Executive Summary 

The ability to simulate aerodynamic flows using computational fluid dynamics (CFD) has progressed rapidly during 

the last several decades and has fundamentally changed the 

aerospace design process. Advanced simulation capabilities 

not only enable reductions in ground-based and in-flight 

testing requirements, but also provide added physical insight, enable superior designs at reduced cost and risk, and 

open new frontiers in aerospace vehicle design and performance. Throughout the evolution of physics-based simulation technologies in general, and computational fluid dynamics methods in particular, NASA’s Aeronautics Research Mission Directorate has played a leading role in the 

development and deployment of these technologies. However, today the aerospace CFD community finds itself at a 

crossroads due to the convergence of several factors. In 

spite of considerable successes, reliable use of CFD has 

remained confined to a small but important region of the 

operating design space due to the inability of current methods to reliably predict turbulent-separated flows. At the 

same time, High Performance Computing (HPC) hardware 

is progressing rapidly and is on the cusp of a paradigm shift 

in technology that may require a rethinking of current CFD 

algorithms and software. Finally, during the last decade, 

government investment in simulation-based technology for 

aerospace applications has been significantly reduced and 

access to leading-edge HPC hardware has been constrained 

both in government and industry. Sustaining future advances in CFD and related multidisciplinary analysis and optimization tools will be critical for achieving NASA’s aeronautics goals, invigorating NASA’s space program, keeping 

industry competitive, and advancing aerospace engineering 

in general. The improvement of a simulation-based engineering design process in which CFD plays a critical role is 

a multifaceted problem that requires a comprehensive longterm, goal-oriented research strategy. The objective of this 

report is to develop such a plan, based on factual information, expert knowledge, community input, and in-depth 

experience. 

This report represents the findings and recommendations of a 

multidisciplinary team that was assembled in response to a 

NASA Research Announcement (NRA) with the goal of 

formulating a knowledge-based forecast and research strategy for developing a visionary CFD capability in the notional 

year 2030. The diverse team members bring together deep 

expertise in the areas of aerodynamics, aerospace engineering, applied mathematics, and computer science, and the 

team includes members with extensive experience from industry, academia, and government. A multipronged strategy 

was adopted for gathering information and formulating a 

comprehensive research plan. Input from the broader international technical community was sought, and this was obtained initially through the development and compilation of 

an online survey that garnered more than 150 responses. As a 

follow-up, a workshop was held with academic, industrial, 

and government participants from the general aerospace engineering community with a stake in simulation-based engineering. The results from the survey and workshop were synthesized and refined by the team, with considerable additions 

through internal discussions and feedback from sponsoring 

NASA officials. The overall project spanned a period of 12 

months and resulted in a series of findings, a vision for the 

capabilities required in the year 2030, and a set of recommendations for achieving these capabilities. 

Findings

1. NASA investment in basic research and technology 

development for simulation-based analysis and design has declined significantly in the last decade and 

must be reinvigorated if substantial advances in 

simulation capability are to be achieved. Advancing 

simulation capabilities will be important for both national aeronautics and space goals, and has broad implications for national competitiveness. This will require advances in foundational technologies, as well as 

increased investment in software development, since 

problem and software complexity continue to increase 

exponentially. 

2. HPC hardware is progressing rapidly and technologies that will prevail are difficult to predict. However, 

there is a general consensus that HPC hardware is on the 

cusp of a paradigm shift that will require significantly 

new algorithms and software in order to exploit emerging hardware capabilities. While the dominant trend is 

toward increased parallelism and heterogeneous architectures, alternative new technologies offer the potential 

for radical advances in computational capabilities, although these are still in their infancy. 

3. The use of CFD in the aerospace design process is 

severely limited by the inability to accurately and reliably predict turbulent flows with significant regions 

of separation. Advances in Reynolds-averaged NavierStokes (RANS) modeling alone are unlikely to overcome this deficiency, while the use of Large-eddy simulation (LES) methods will remain impractical for various 

important applications for the foreseeable future, barring 

any radical advances in algorithmic technology. Hybrid 

RANS-LES and wall-modeled LES offer the best prospects for overcoming this obstacle although significant 

modeling issues remain to be addressed here as well. 

Furthermore, other physical models such as transition 

and combustion will remain as pacing items. 

4. Mesh generation and adaptivity continue to be significant bottlenecks in the CFD workflow, and very little government investment has been targeted in these 

areas. As more capable HPC hardware enables higher 

resolution simulations, fast, reliable mesh generation and 

adaptivity will become more problematic. Additionally, 

adaptive mesh techniques offer great potential, but have 
2 

not seen widespread use due to issues related to software 

complexity, inadequate error estimation capabilities, and 

complex geometries. 

5. Revolutionary algorithmic improvements will be required to enable future advances in simulation capability. Traditionally, developments in improved discretizations, solvers, and other techniques have been as important as advances in computer hardware in the development of more capable CFD simulation tools. However, a lack of investment in these areas and the supporting 

disciplines of applied mathematics and computer science 

have resulted in stagnant simulation capabilities. Future 

algorithmic developments will be essential for enabling 

much higher resolution simulations through improved 

accuracy and efficiency, for exploiting rapidly evolving 

HPC hardware, and for enabling necessary future error 

estimation, sensitivity analysis, and uncertainty quantification techniques. 

6. Managing the vast amounts of data generated by 

current and future large-scale simulations will continue to be problematic and will become increasingly 

complex due to changing HPC hardware. These include effective, intuitive, and interactive visualization of 

high-resolution simulations, real-time analysis, management of large databases generated by simulation ensembles, and merging of variable fidelity simulation data 

from various sources, including experimental data. 

7. In order to enable increasingly multidisciplinary 

simulations, for both analysis and design optimization purposes, advances in individual component 

CFD solver robustness and automation will be required. The development of improved coupling at high 

fidelity for a variety of interacting disciplines will also 

be needed, as well as techniques for computing and coupling sensitivity information and propagating uncertainties. Standardization of disciplinary interfaces and the 

development of coupling frameworks will increase in 

importance with added simulation complexity. 

Vision 

A knowledge-based vision of the required capabilities of 

state-of-the-art CFD in the notional year 2030 is developed 

in this report. The Vision 2030 CFD capability is one that: 

 Is centered on physics-based predictive modeling. 

 Includes automated management of errors and uncertainties. 

 Provides a much higher degree of automation in all steps 

of the analysis process. 

 Is able to effectively leverage the most capable HPC 

hardware of the day. 

 Has the flexibility to tackle large-scale capability tasks 

in a research environment but can also manage large 

numbers of production jobs for database applications. 

 Seamlessly integrates with other disciplinary codes for 

enabling complex multidisciplinary analyses and optimizations. 

The Vision includes a much higher level of integration between advanced computational methods and improved 

ground-based and flight test techniques and facilities in order 

to best advance aerospace product development efforts and 

reduce technical risk in the future. 

A number of Grand Challenge (GC) problems are used that 

constitute the embodiment of this vision of the required CFD 

capabilities in 2030, and cover all important application areas 

of relevance to NASA’s aeronautics mission as well as important aspects of NASA’s space exploration mission. Four 

GC problems have been identified: 

1. Wall resolved LES simulation of a full powered aircraft configuration in the full flight envelope 

2. Off-design turbofan engine transient simulation 

3. Multidisciplinary Analysis and Optimization (MDAO) 

of a highly flexible advanced aircraft configuration 

4. Probabilistic analysis of a powered space access configuration 

These Grand Challenge problems are chosen because they 

are bold and will require significant advances in HPC usage, physical modeling, algorithmic developments, mesh 

generation and adaptivity, data management, and multidisciplinary analysis and optimization to become feasible. In 

fact, they may not be achievable in the 2030 time frame, but 

are used as drivers to identify critical technologies in need 

of investment and to provide benchmarks for continually 

measuring progress toward the long-term goals of the research program. 

Recommendations 

In order to achieve the Vision 2030 CFD capabilities, a 

comprehensive research strategy is developed. This is formulated as a set of recommendations which, when considered together, result in a strategy that targets critical disciplines for investment, while monitoring progress toward the 

vision. Two types of recommendations are made: a set of 

specific programmatic recommendations and a series of 

more general strategic recommendations. The programmatic recommendations avoid the identification of specific 

technologies and the prescription of funding levels, since 

these decisions are difficult at best given the long-range 

nature of this planning exercise. Rather, long-range objectives are identified through the vision and GC problems, 

and a set of six general technology areas that require sustained investment is described. A mechanism for prioritizing current and future investments is suggested, based on 

the periodic evaluation of progress toward the GC problems. 
3 

Programmatic Recommendation 1: NASA should develop, fund, and sustain a base research and technology 

(R&T) development program for simulation-based analysis and design technologies. The presence of a focused base 

R&T program for simulation technologies is an essential 

component of the strategy for advancing CFD simulation 

capabilities. This recommendation consists of expanding the 

current Revolutionary Computational Aerosciences (RCA) 

program and organizing it around six technology areas identified in the findings: 

1. High Performance Computing (HPC) 

2. Physical Modeling 

3. Numerical Algorithms 

4. Geometry and Grid Generation 

5. Knowledge Extraction 

6. MDAO 

The physical modeling area represents an expansion of the 

current turbulence modeling area under the RCA program 

to encompass other areas such as transition and combustion, 

while the numerical algorithms area corresponds to a current emphasis in the RCA program that must be broadened 

substantially. The other areas constitute new, recommended 

thrust areas within the RCA program. 

Programmatic Recommendation 2: NASA should develop and maintain an integrated simulation and software 

development infrastructure to enable rapid CFD technology maturation. A leading-edge in-house simulation capability is imperative to support the necessary advances in CFD 

required for meeting the 2030 vision. Maintaining such a 

capability will be crucial for understanding the principal 

technical issues and overcoming the impediments, for investigating new techniques in a realistic setting, and for engaging with other stakeholders. In order to be sustainable, dedicated resources must be allocated toward the formation of a 

streamlined and improved software development process that 

can be leveraged across various projects, lowering software 

development costs, and releasing researchers and developers 

to focus on scientific or algorithmic implementation aspects. 

At the same time, software standards and interfaces must be 

emphasized and supported whenever possible, and open 

source models for noncritical technology components should 

be adopted. 

Programmatic Recommendation 3: NASA should utilize 

and optimize HPC systems for large-scale CFD development and testing. Access to large-scale HPC hardware is 

critical for devising and testing the improvements and novel 

algorithms that will be required for radically advancing CFD 

simulation capabilities. Although the current NASA paradigm favors computing for many small, production jobs 

(“capacity”) over larger, proof-of-concept jobs (“capability”), 

a mechanism must be found to make large-scale HPC hardware available on a regular basis for CFD and multidisciplinary simulation software development at petascale to exascale levels and beyond. This may be done through internal 

reallocation of resources, sharing with other NASA mission 

directorates, leveraging other government agency HPC assets, or through any combination of these approaches. 

Programmatic Recommendation 4: NASA should lead 

efforts to develop and execute integrated experimental 

testing and computational validation campaigns. Systematic numerical validation test datasets and effective mechanisms to disseminate validation results are becoming more 

important as CFD complexity increases. NASA is ideally 

positioned to lead such efforts by leveraging its unique experimental facilities in combination with its extensive in-house 

CFD expertise, thus contributing valuable community resources that will be critical for advancing CFD technology. 

The development of new experimental testing technologies 

and facilities is expected to play a continuing role not just in 

aerospace product development, but increasingly in computational method validation. 

Strategic Recommendation 5: NASA should develop, foster, and leverage improved collaborations with key research partners and industrial stakeholders across disciplines within the broader scientific and engineering 

communities. In an environment of limited resources, 

achieving sustained critical mass in the necessary simulation 

technology areas will require increased collaborations with 

other stakeholders. Mutually beneficial collaborations are 

possible between NASA mission directorates, as well as with 

other US government agencies with significant ongoing investments in computational science. Tighter collaboration 

with industry, specifically in simulation technology areas, 

would also be beneficial to both parties and a joint Computational Science Leadership team is proposed to coordinate 

such collaborations. At the same time, investments must look 

beyond the traditional aerospace engineering disciplines to 

drive substantial advances in simulation technology, and 

mechanisms for engaging the wider scientific community, 

such as focused research institutes that engage the broader 

academic community, should be explored. 

Strategic Recommendation 6: NASA should attract 

world-class engineers and scientists. The ability to achieve 

the long-term goals for CFD in 2030 is greatly dependent on 

having a team of highly educated and effective engineers and 

scientists devoted to the advancement of computational sciences. Mechanisms for engaging graduate and undergraduate 

students in computational science with particular exposure to 

NASA aeronautics problems must be devised. These include 

student fellowships, as well as visiting programs and internships, which may be facilitated through external institutes 

and centers. 
4 

2 Introduction 

The rapid advance of computational fluid dynamics (CFD) 

technology during the last several decades has fundamentally 

changed the aerospace design process. Aggressive use of 

CFD is credited with drastic reductions in wind tunnel time 

for aircraft development programs1-4, as well as lower numbers of experimental rig tests in gas turbine engine development programs.5-6 CFD has also enabled the design of highspeed, access-to-space, and re-entry vehicles in the absence 

of suitable ground-based testing facilities.7-9 In addition to 

reducing testing requirements, physics-based simulation 

technologies such as CFD offer the added potential of delivering superior understanding and insight into the critical 

physical phenomena limiting component performance, thus 

opening new frontiers in aerospace vehicle design.10-11

Physics-based simulations in general, and CFD in particular, 

are front and center in any aerospace research program since 

these are crosscutting technologies that impact all speed regimes and all vehicle classes. This is evidenced in the National Research Council (NRC) commissioned decadal survey on aeronautics12 which identifies five common themes 

across the entire aeronautics research enterprise, the first two 

being physics-based simulation and physics-based design 

tools. Similarly, these technologies affect all of the outcomes 

in the current National Aeronautics R&D Plan,13 and continued advances in these technologies will be critical for meeting the stated outcomes. 

Since the advent of scientific computing, NASA’s Aeronautics Research Mission Directorate (ARMD) has played a 

leading role in the development and deployment of CFD 

technologies.14 Successive external reviews of NASA Aeronautics programs during the last two decades by organizations such as the National Academy of Engineering (NAE)

and others12 have repeatedly praised the world-class status 

and leading-edge technical contributions of the simulationbased engineering tools developed under these programs. In 

fact, many algorithms, techniques, and software tools in use 

today within and beyond the aerospace industry can trace 

their roots back to NASA development or funding. 

The development of computational aerodynamics has been 

characterized by a continual drive to higher fidelity and more 

accurate methods from the 1970s to the 1990s, beginning 

with panel methods, proceeding to linearized and nonlinear 

potential flow methods, inviscid flow (Euler) methods, and 

culminating with Reynolds-averaged Navier-Stokes (RANS) 

methods. These advances were arrived at through sustained 

investment in methodology development coupled with acquisition and deployment of leading edge High Performance 

Computing (HPC) hardware made available to researchers.15

While Moore’s law has held up remarkably well, delivering a 

million-fold increase in computational power during the last 

20 years, there is also ample evidence that equivalent or 

greater increases in simulation capabilities were achieved 

through the development of advanced algorithms within the 

same time frame.1,16-18

However, the last decade has seen stagnation in the capabilities used in aerodynamic simulation within the aerospace 

industry, with RANS methods having become the highfidelity method of choice and advances due mostly to the use 

of larger meshes, more complex geometries, and more numerous runs afforded by continually decreasing hardware 

costs.19-23 At the same time, the well-known limitations of 

RANS methods for separated flows have confined reliable 

use of CFD to a small region of the flight envelope or operating design space.24 Simultaneously, algorithmic development 

has been substantially scaled back within NASA and access 

to leading-edge HPC hardware has been constrained, both at 

NASA and within industry.25 In some sense, current CFD has 

become a commodity based on mature technology, suitable 

only for commodity hardware and reliable only for problems 

for which an extensive experience base exists. 

Continued advances in physics-based simulation technologies in general, and CFD in particular, are essential if NASA 

is to meet its aeronautics research goals, as well as for successfully advancing the outcomes in the National Aeronautics R&D plan.13 The required advances in fuel burn, 

noise, emissions, and climate impact will only be realized 

with vastly more sophisticated analysis of future configurations. Beyond Aeronautics, NASA’s space missions rely 

heavily on computational tools developed within ARMD7-9, 

26-30 and superior designs at lower cost and risk will require 

radical advances in new CFD tools.31 Additionally, the loss 

of the leadership role NASA ARMD once played in the development of simulation-based engineering technology has 

larger implications for the aerospace industry in particular, 

and national competitiveness in general.17,32,33 Due to the 

long lead times and high risk involved, industry must rely on 

government agencies to develop and demonstrate new simulation technologies at large scale, after some investment in 

proof-of-concept at universities. In recent years, the National 

Science Foundation (NSF) and Department of Energy (DOE) 

have led investing in computational science-based research 

and in deploying leading-edge HPC facilities, although with 

a different focus based more on scientific discovery rather 

than engineering product design.16, 18, 34-36 As noted by a blueribbon panel report convened by the NSF, simulation-based 

engineering is fundamentally different from science-based 

simulation and is in danger of being neglected under the current scenario, with important implications for national competitiveness.37, 38

Thus, there is a national imperative to reinvigorate the investment in physics-based engineering simulation tools in 

general, and in CFD in particular, and NASA is uniquely 

positioned to fill this role. In addition to enhancement of 

CFD technology, effective use of existing, and potentially 

new, ground-based testing facilities will be required to provide a complementary set of tools to best advance aerospace 
5 

product development efforts and reduce technical risk in the 

future. Sustaining future advances in CFD and related multidisciplinary analysis and optimization tools along with strong 

support of ground-based and flight testing technologies and 

facilities will be key for achieving NASA next generation 

aeronautics goals, keeping industry competitive, invigorating 

NASA’s space program, and advancing aerospace engineering. With investment, the resulting engineering design process would decrease risk, reduce time-to-market, improve 

products, and facilitate truly revolutionary aerospace vehicles 

through the ability to consider novel designs. Without such 

an investment, the engineering design process will look much 

the same in 2030 as it does today and act as a barrier to revolutionary advances in aerospace and other industries of national importance. 

The improvement of a simulation-based engineering design 

process in which CFD plays a critical role is a multifaceted 

problem. Having relied on mature algorithms and ridden the 

wave of ever-decreasing commodity computer hardware 

costs, the CFD development community now finds itself 

poorly positioned to capitalize on the rapidly changing HPC 

architectures, which include massive parallelism and heterogeneous architectures.38-40 New paradigms will be required to 

harness the rapidly advancing capabilities of new HPC hardware.41, 42 At the same time, the scale and diversity of issues 

in aerospace engineering are such that increases in computational power alone will not be enough to reach the required 

goals, and new algorithms, solvers, physical models, and 

techniques with better mathematical and numerical properties 

must be developed.1,16-18 Finally, software complexity is increasing exponentially, slowing adoption of novel techniques 

into production codes and shutting out production of new 

software development efforts, while simultaneously complicating the coupling of various disciplinary codes for multidisciplinary analysis and design.43 The development of a 

long-range research plan for advancing CFD capabilities 

must necessarily include all these considerations, along with 

the larger goal of comprehensive advances in multidisciplinary analysis and optimization capabilities. 

The objective of this study is to develop such a plan, based 

on factual information, expert knowledge, and the in-depth 

experience of the team and the broader community. The 

strategy begins by defining the required capabilities for CFD 

in the notional year 2030. By contrasting this vision with the 

current state, we identify technical impediments and formulate a technology development plan. This in turn is used to 

develop a research strategy for achieving the goals of the 

Vision 2030 CFD capability. The outcome of the research 

plan is a set of recommendations formulated to enable the 

successful execution of the proposed strategy. 

3 Vision of CFD in 2030 

Given the inherent difficulties of long-term predictions, our 

vision for CFD in 2030 is grounded on a desired set of capabilities that must be present for a radical improvement in 

CFD predictions of critical flow phenomena associated with 

the key aerospace product/application categories, including 

commercial and military aircraft, engine propulsion, rotorcraft, space exploration systems, launch vehicle programs, 

air-breathing space-access configurations, and spacecraft 

entry, descent, and landing (EDL). 

This set of capabilities includes not only the accurate and 

efficient prediction of fluid flows of interest, but also the 

usability of CFD in broader contexts (including uncertainty 

quantification, optimization, and multidisciplinary applications) and in streamlined/automated industrial analysis and 

design processes. To complicate things further, CFD in 2030 

must effectively leverage the uncertain and evolving environment of HPC platforms that, together with algorithmic 

improvements, will be responsible for a large portion of the 

realized improvements. 

The basic set of capabilities for Vision 2030 CFD must include, at a minimum: 

1. Emphasis on physics-based, predictive modeling. In 

particular, transition, turbulence, separation, chemically 

reacting flows, radiation, heat transfer, and constitutive 

models must reflect the underlying physics more closely 

than ever before. 

2. Management of errors and uncertainties resulting from 

all possible sources: (a) physical modeling errors and 

uncertainties addressed in item #1, (b) numerical errors 

arising from mesh and discretization inadequacies, and 

(c) aleatory uncertainties derived from natural variability, as well as epistemic uncertainties due to lack of 

knowledge in the parameters of a particular fluid flow 

problem. 

3. A much higher degree of automation in all steps of the 

analysis process is needed including geometry creation, 

mesh generation and adaptation, the creation of large databases of simulation results, the extraction and understanding of the vast amounts of information generated, 

and the ability to computationally steer the process. Inherent to all these improvements is the requirement that 

every step of the solution chain executes high levels of 

reliability/robustness to minimize user intervention. 
6 

4. Ability to effectively utilize massively parallel, heterogeneous, and fault-tolerant HPC architectures that will 

be available in the 2030 time frame. For complex physical models with nonlocal interactions, the challenges of 

mapping the underlying algorithms onto computers with 

multiple memory hierarchies, latencies, and bandwidths 

must be overcome. 

5. Flexibility to tackle capability- and capacity-computing 

tasks in both industrial and research environments so 

that both very large ensembles of reasonably-sized solutions (such as those required to populate full-flight envelopes, operating maps, or for parameter studies and design optimization) and small numbers of very-largescale solutions (such as those needed for experiments of 

discovery and understanding of flow physics) can be 

readily accomplished. 

6. Seamless integration with multidisciplinary analyses that 

will be the norm in 2030 without sacrificing accuracy or 

numerical stability of the resulting coupled simulation, 

and without requiring a large amount of effort such that 

only a handful of coupled simulations are possible. 

Included in this desired set of capabilities is a vision for how 

CFD in 2030 will be used: a vision of the interaction between 

the engineer/scientist, the CFD software itself, its framework 

and all the ancillary software dependencies (databases, modules, visualization, etc.), and the associated HPC environment. A single engineer/scientist must be able to conceive, 

create, analyze, and interpret a large ensemble of related simulations in a time-critical period (e.g., 24 hours), without 

individually managing each simulation, to a pre-specified 

level of accuracy. There should be less emphasis on the mechanics of running and collecting the information, and more 

emphasis on interpreting and understanding the results of the 

work. Like the predictive nature of large-scale, finiteelement-based, linear structural analyses that are assumed in 

the aerospace industry, information derived from computations of fluid flow must carry the same stamp of approval or, 

at least, a reasonable estimate of possible errors contained in 

the information provided. At the moment, CFD is not yet 

sufficiently predictive and automated to be used in critical/relevant engineering decisions by the non-expert user, 

particularly in situations where separated flows are present. 

Additionally, the Vision includes a much higher level of integration between advanced computational methods and improved ground-based and flight test techniques and facilities 

in order to best advance aerospace product development efforts and reduce technical risk in the future. 

Finally, as part of our vision, we define a set of Grand Challenge (GC) problems (as shown in the graphic on the next 

page) that are bold and in fact may not be solvable in the 

2030 timeframe, but are used as drivers to identify critical 

technologies in need of investment, and to serve as benchmarks for continually measuring progress toward the longterm development goals. These GC problems were chosen 

to embody the requirements for CFD in 2030, and cover all 

important application areas of relevance to NASA’s aeronautics mission, as well as important aspects of NASA’s 

space exploration mission. Details on the GC problems are 

presented in Section 6. 

4 Current State 

At present, CFD is used extensively in the aerospace industry 

for the design and analysis of air and space vehicles and 

components. However, the penetration of CFD into aerospace design processes is not uniform across vehicle types, 

flight conditions, or across components. CFD often plays a 

complementary role to wind tunnel and rig tests, engine certification tests, and flight tests by reducing the number of test 

entries and/or reducing testing hours.3-5 But, in many circumstances, CFD provides the only affordable or available source 

of engineering data to use in product design due to limitations either with model complexity and/or wind tunnel capability, or due to design requirements that cannot be addressed 

with ground-based testing of any kind.8, 10, 31 As a result, CFD 

technology development has been critical in not only minimizing product design costs, but also in enabling the design 

of truly novel platforms and systems. 

Critical Flow Phenomena Addressed in This Study 

• Flow separation: e.g., smooth-body, shock-induced, blunt/bluff body 

• Laminar to turbulent boundary layer flow transition/reattachment 

• Viscous wake interactions and boundary layer confluence 

• Corner/junction flows 

• Icing and frost 

• Circulation and flow separation control 

• Turbomachinery flows 

• Aerothermal cooling/mixing flows 

• Reactive flows, including gas chemistry and combustion 

• Jet exhaust 

• Airframe noise 

• Vortical flows: wing/blade tip, rotorcraft 

• Wake hazard reduction and avoidance 

• Wind tunnel to flight scaling 

• Rotor aero/structural/controls, wake and multirotor interactions, acoustic 

loading, ground effects 

• Shock/boundary layer, shock/jet interactions 

• Sonic boom 

• Store/booster separation 

• Planetary retro-propulsion 

• Aerodynamic/radiative heating 

• Plasma flows 

• Ablator aerothermodynamics 

• Plasma flows 
7 

Generally, the design process is composed of three key phases: conceptual design, preliminary and detailed design, and 

product validation. The current usage of CFD tools and processes in all three of these design phases is summarized below. 

Conceptual Design. CFD is often used in the early, conceptual design of products where it has been both previously calibrated for similar applications using data-morphing 

techniques, as well as for new configurations where little 

or no engineering data is available to guide design decisions. Simplified models are typically used during the conceptual optimization phase to allow reasonably accurate 

trades to be made between drag, fuel consumption, weight, 

payload/range, thrust, or other performance measures. Use 

of simplified models is necessary to allow often timeconsuming optimization processes to be used in the overall 

design effort, but inherently places conservatism into the 

final design. This conservatism derives from the use of 

models that are too similar within the existing product design space, other geometric simplifications, or the use of 

low-fidelity CFD tools that trade off flow physics modeling accuracy for execution speed. 

Preliminary/Detailed Design. Once a product development program is launched, CFD is a necessary and uniformly present tool in the detailed configuration design 

process. For example, CFD is indispensable in the design 

of cruise wings in the presence of nacelles for commercial 

airplanes, and for inlet and nozzle designs; wind tunnels 

are used to confirm the final designs.1,4 In both military and 

commercial aircraft design processes, CFD is the primary 

source of data for aircraft load distributions and ground effect estimations.10 Similarly, gas turbine engine manufacturers rely on CFD to predict component design performance, having reduced the number of single-component 

rigs substantially as CFD capability has become more mature.5,6 Increasingly, multicomponent and multiphysics 

simulations are performed during the design cycle, but the 

long clock times often associated with these processes restricts their widespread adoption. For space exploration, 

CFD is often used to gain important insight into flow physics (e.g., multiple plume interactions) used to properly locate external components on the surface of launch vehicles 

or spacecraft.9,27,29 CFD is also increasingly providing substantial portions of the aero and propulsion performance 

database.7,9,30 In many cases, wind tunnel data is used only 

to anchor the CFD data at a few test points to provide confidence in the CFD database. CFD is the primary source of 

data for the hypersonic flight regime when ground testing 

is limited or does not exist.8, 44 

Product Validation and Certification. As the product 

development process moves into the validation phase and 

certification testing, CFD is often used to confirm performance test results, assess the redesign of components that 

show potential for improved performance, and to answer 

any other questions that arise during product testing. Typically, product configurations evolve over the testing period 

based on a combination of measured results and engineering judgment bolstered by the best simulation capability 

available. In general, CFD modeling capability grows to 

capture the required scope and physics to answer the questions raised during testing. The expense of responding to 

often unplanned technical surprises—which results in more 

time on the test stand or in flight test, or changes in hardware—drives conservatism into aerospace designs and is a 

significant motivation for improving the accuracy and 

speed of CFD. If CFD is sufficiently accurate and fast, engineers can move from their traditional design space with 

greater confidence and less potential risk during testing. 

For each of these design phases, the performance (in terms 

of numerical efficiency and solution accuracy) of CFD is of 

critical importance. A high-level view of the current state of 

CFD in several key technical areas is given below. 

High Performance Computing (HPC). The effectiveness 

and impact of CFD on the design and analysis of aerospace 

products and systems is largely driven by the power and 

availability of modern HPC systems. During the last decades, CFD codes were formulated using message passing 

GC1 LES of powered aircraft configuration 

across the full 

flight envelope

GC2 Off-design turbofan engine transient 

simulation

GC3 MDAO of a highly-flexible advanced 

aircraft configuration

GC4 Probabilistic analysis of a powered 

space access configuration

255606.002.ppt

Grand Challenge Problems
8 

(e.g., MPI) and thread (e.g., OpenMP) software models for 

expressing parallelism to run as efficiently as possible on 

current generation systems. However, with the emergence 

of truly hierarchical memory architectures having numerous graphical processing units (GPUs) and coprocessors, 

new CFD algorithms may need to be developed to realize 

the potential performance offered by such systems. Government labs, such as Oak Ridge National Lab (ORNL), 

Argonne National Lab (ANL), and the NASA Advanced 

Supercomputing (NAS) facility at NASA Ames Research 

Center, have often led the way with the acquisition and 

testing of new hardware. Much research on testing and tailoring of CFD algorithms takes place on these platforms 

with heavy participation from academia, national labs and 

to some extent industry as well. Government computing 

resources are also used to tackle large-scale calculations of 

challenge problems, such as the detailed direct numerical 

simulation (DNS) of spray injector atomization or high fidelity simulations of transition and turbulent separation in 

turbomachinery. However, because of the high cost of 

these leadership-class systems, industry and academia often purchase smaller commodity clusters utilizing similar 

types of processors when the latest hardware technology is 

fully demonstrated on CFD problems and other important 

applications. 

Turbulence Modeling. Current practices for CFD-based 

workflows utilize steady Reynolds-average Navier-Stokes 

(RANS) with 1- or 2-equation turbulence models,46-48 although hybrid unsteady RANS/LES methods are increasingly common for certain classes of simulations in which 

swirling and intentionally separated flows are dominant, 

such as combustors. Techniques to combine near-wall 

RANS regions and outer flow field, large-eddy simulation 

(LES) regions in these hybrid methods are immature. 

Many CFD design processes include an estimation of 

boundary layer transition, using a range of models, from 

purely empirical to coupled partial-differential equation 

(PDE) solutions of stability equations.49, 50 Both approaches involve much empiricism, may be missing some 

modes of transition, and are evolving. As a result, no 

generalized transition prediction capability is in widespread use in Navier-Stokes CFD, and the default practice is to run the codes “fully turbulent”. Steady-state 

CFD accounts for a vast majority of simulations; unsteady 

flow predictions are inherently more expensive and not yet 

uniformly routine in the design process, with some exceptions.51

Process Automation. Current CFD workflows are often 

paced by the geometry preprocessing and grid generation 

phases, which are significant bottlenecks. In some cases, 

where the design effort involves components of similar 

configurations, specialized, automated processes are built 

that considerably reduce set-up time, execution of the 

CFD solver, and post-processing of results. This process 

to production capability of the CFD workflow only occurs in areas where the design work is routine and the investment in automation makes business sense; singleprototype designs and novel configurations continue to 

suffer the pacing limits of human-in-the-loop workflows 

because the payoff for automating is not evident. This issue is not unique to the aerospace industry. 

Solution Uncertainty and Robustness. In practice, CFD 

workflows contain considerable uncertainty that is often 

not quantified. Numerical uncertainties in the results come 

from many sources, including approximations to geometry, 

grid resolution, problem setup including flow modeling 

and boundary conditions, and residual convergence. Although NASA and professional organizations such as 

ASME and AIAA have created standards for the verification and validation of CFD and heat transfer analyses52-54, 

such techniques are not widely used in the aerospace industry. With a few notable exceptions, CFD is carried out 

on fixed grids that are generated using the best available 

practices to capture expected flow features, such as attached boundary layers.55 Such approaches cannot reliably 

provide adequate resolution for flow features when locations are not known a priori, such as shocks, shear layers, 

and wakes. Although grid refinement is often seen as a 

panacea to addressing grid resolution issues, it is seldom 

done in practice (with the exception of a few workshop test 

cases) because uniform refinement is impractical in 3D. 

Adaptive mesh refinement strategies offer the potential for 

superior accuracy at reduced cost, but have not seen widespread use due to robustness, error estimation, and software complexity issues. Achieving consistent and reliable 

flow solver or residual convergence remains problematic in 

many industrial cases. Although many CFD codes are able 

to demonstrate convergence for a few simple problems, for 

many flows involving difficult flow physics and/or complex geometries such as an aircraft in high-lift configuration, many of the current solver techniques employed are 

not strong enough to ensure robust convergence.56 Engineering judgment is required to interpret results that are not 

well converged, which introduces conservatism into decision-making. Furthermore, the use of steady-state flow 

solvers itself is in question for many flows of engineering 

interest. 

Multidisciplinary Analysis and Optimization (MDAO).

Although the basic concepts of MDAO are fairly well accepted in the community, the routine use of MDAO methods is not, by any means, pervasive. At moderate levels of 

fidelity (commensurate with analyses conducted during the 

conceptual design phase), it is common industrial practice 

to perform coupled multidisciplinary analyses (MDA) of 

the most tightly integrated disciplines in a design. Aerostructural analyses, conjugate heat transfer calculations, 

and aero-acoustic simulations all tend to take place in aircraft, spacecraft, jet engine, and rotorcraft analysis and design processes. High fidelity CFD is not routinely used in 

such MDAs, although recent years have witnessed a signif-
9 

icant rise in the coupling of state-of-the-art CFD with additional disciplines. While frameworks for the coupling of 

disciplinary analyses are widely available,57-60 the ability to 

couple CFD with other high fidelity descriptions of participating disciplines is limited by the availability of coupling 

software and, more fundamentally, by a lack of general 

methodologies for accurate, stable, and conservative 

MDAs. The application of optimization techniques in industry is mostly limited to single-discipline simulations. 

Although conceptual design tools have long benefited from 

multidisciplinary optimization (MDO) approaches (with 

various modules at the lowest fidelity levels), high fidelity 

CFD-based optimizations are still rare. During the past 

decade, the development of advanced surrogate modeling 

techniques and the introduction of adjoint-based optimal 

shape design techniques have enabled the use of CFD in 

aerodynamic optimization of aircraft and gas turbine components. However, the use of optimization with multiple 

disciplines treated using high-fidelity methods is still within the realm of advanced research and is by no means a 

routine practice. 

5 CFD Technology Gaps and Impediments 

Given the current state of CFD technology, tools, and processes described above, necessary research and development to address gaps and overcome impediments in CFD 

technology are fundamental to attaining the vision for CFD 

in 2030 outlined earlier. Five key technical areas were identified during this Vision 2030 study and rose to the highest 

level of importance as identified from a user survey and 

workshop of a large international community of CFD researchers and practitioners. In the subsections below, the 

effective utilization of HPC is first considered. This includes both the implications of future computing platforms 

and the requirements imposed by potential emerging future 

programming paradigms to deal with exascale challenges. 

Next, we describe the desired level of capability (in 2030) 

for the prediction of unsteady, turbulent flows including 

transition and separation. We continue with a discussion of 

research topics in autonomous and reliable CFD simulation 

techniques that aim at providing both a high level of automation in the analysis process and the required algorithms 

(both for meshing and the solution process) to ensure confidence in the outcomes. Then, in order to derive useful information from the simulations, the discussion on smart 

knowledge extraction from large-scale databases and simulations considers the research required to automate the process of sifting through large amounts of information, often 

at a number of different geographic locations, and extracting patterns and actionable design decisions. Finally, we 

end with a discussion on multidisciplinary and multiphysics 

simulations that describes the research work required to 

perform seamless, accurate, and robust simulations of multiphysics problems in which CFD would be an integral part. 

5.1 Effective Utilization of High-Performance 

Computing (HPC) 

CFD in 2030 will be intimately related to the evolution of the 

computer platforms that will enable revolutionary advances 

in simulation capabilities. The basic framework for Vision 

2030 CFD must map well to the relevant future programming 

paradigms, which will enable portability to changing HPC 

environments and performance without major code rework.41

However, the specific architecture of the computing platforms that will be available is far from obvious. We can, 

however, speculate about the key attributes of such machines 

and identify key technology gaps and shortcomings so that, 

with appropriate development, CFD can perform at future 

exascale levels on the HPC environments in 2030. 

Hybrid computers with multiple processors and accelerators 

are becoming widely available in scientific computing and, 

although the specific composition of a future exascale computer is not yet clear, it is certain that heterogeneity in the 

computing hardware, the memory architecture, and even the 

network interconnect will be prevalent. Future machines 

will be hierarchical, consisting of large clusters of sharedmemory multiprocessors, themselves including hybrid-chip 

multiprocessors combining low-latency sequential cores 

with high-throughput data-parallel cores. Even the memory 

chips are expected to contain computational elements, 

which could provide significant speedups for irregular 

memory access algorithms, such as sparse matrix operations 

arising from unstructured datasets. With such a running 

target on the horizon, the description of 2030 CFD is 

grounded on a target supercomputer that incorporates all of 

the representative challenges that we envision in an exascale supercomputer. These challenges are certainly related to heterogeneity, but more concretely, may include multicore CPU/GPU interactions, hierarchical and specialized 

networks, longer/variable vector lengths in the CPUs, 

shared memory between CPU and GPUs, and even a higher 

utilization of vector units in the CPUs. Research must be 

conducted so that we are ready to tackle the specific challenges presented. 

The wildcard in predicting what a leading edge HPC system 

will look like is whether one or more of several current nascent HPC technologies will come to fruition. Radical new 

technologies such as quantum computing, superconducting 

logic, low-power memory, massively parallel molecular 

computing, next generation “traditional” processor technologies, on-chip optics, advanced memory technologies (e.g., 

3D memory) have been proposed but are currently at very 

low technology readiness levels (TRL). Many of these 

revolutionary technologies will require different algorithms, 

software infrastructures, as well as different ways of using 

results from CFD simulations.61
10 

Stampede (USA: University of Texas)

System

Site

Titan (USA: DOE)

Sequoia (USA: DOE)

K computer (Japan)

Mira (USA: DOE)

JUQUEEN (Germany)

Vulcan (USA: DOE)

SuperMUC (Germany)

Tianhe-1A (China)

Pleiades (USA: NASA

5.2

LINPACK

(pFLOP/s)

17.6

17.2

10.5

8.6

5.0

4.3

2.9

2.6

1.2

Theoretical Peak

pFLOP/s)

27.1

20.1

11.3

10.1

8.5

5.9

5.0

3.2

4.7

2.9

Top 500

Ranking

Tianhe-2 (China) 33.9 54.9

Cores

560,640

1,572,864

705,024

786,432

462,462

458,752

393,216

147,456

186,368

195,264

1 3,120,000

2

3

4

5

6

7

8

9

10

19

255606.003.ppt

CASE STUDY 1: Current Utilization of HPC at NASA 

HPC utilization at NASA is almost entirely focused on capacity computing (running many, relatively small jobs) with little capability computing (running jobs utilizing a significant amount of a leadership class high performance computer). The largest NASA HPC system is 

Pleiades at the NASA Advanced Supercomputing (NAS) division. As of June 2013, this system is currently ranked 19th in the world in 

terms of its performance on the linear algebra benchmark LINPACK.1 As of October 2013, Pleiades consists of: 

 11,136 nodes with Intel Xeon processors for a total of 162,496 cores 

 64 nodes with NVIDIA graphics processing units for a total of 32,768 cores 

 417 TB of total memory 

From the NAS website, the theoretical peak performance of this configuration is quoted as 2.88 pFLOP/s and the demonstrated 

LINPACK rating is 1.24 pFLOP/s. By comparison, the current fastest system on the Top 500 list is Tianhe-2 at the National University of 

Defense Technology in China that has a theoretical peak performance of 54.9 pFLOP/s and a demonstrated LINPACK rating 33.9 

pFLOP/s. The Top 10 HPC systems are provided in the embedded table, including Pleiades for comparison, and shows that Pleiades is 

a factor of 2 to 30 times slower than these Top 10 systems (in terms of the LINPACK performance). While Pleiades is within a factor of 

about 10 of the world’s fastest HPC systems, it is rarely used at anywhere near its full capability. For example, a snapshot of the Pleiades job queue2 (taken on October 24, 2013 at 2:00PM Eastern) shows the following utilization: 

 469 jobs running 

 Average cores used per job: 457 

 Maximum cores used per job: 5,000 (the only job running more than 1000 cores) 

Thus, although the Pleiades system has approximately 160K CPU cores (and another 32K GPU cores), the average job size is less than 

1K cores and Pleiades is therefore acting as a capacity facility. Further, the usage of Pleiades is over-subscribed with job queues often 

having delays numbering in the days, so that even in its role as a capacity facility, Pleiades is insufficient to meet NASA’s needs. 

By comparison, the DOE has an HPC strategy that encompasses both capacity and capability computing. A key enabler of this strategy 

is the significant HPC resources at the DOE (for example, the DOE has 4 of the Top 10 supercomputer sites shown in the table: Titan, 

Sequoia, Mira, and Vulcan). This wealth of HPC resources allows the DOE to dedicate systems to both capacity and capability computing. For example, DOE leadership systems have job queue policies that (1) strongly favor large jobs that will use a significant fraction of 

a leadership system and (2) limit the potential that these systems are flooded by capacity computations. The DOE also has programs 

such as Innovative and Novel Computational Impact on Theory and Experiment (INCITE)3 specifically designed to encourage capability 

computing. INCITE allocates up to 60% of the Leadership Computing Facilities at Argonne and Oak Ridge National Laboratories to national and international research teams pursuing high-impact research that can demonstrate the ability to effectively utilize a major fraction of these machines in a single job. Utilization data for DOE’s Leadership Facilities bears out the impact these policies have had on 

the pursuit of capability computing. For example, on DOE’s Mira system, which is about four times larger than Pleiades, the average job 

size was 35K cores during the period from April through October 2013. The smallest job size during that time was 8K cores while the 

largest job size used essentially the entire system at nearly 800K cores. Comparisons can also be made between Pleiades and DOE’s 

“Intrepid” system. Intrepid is the 58th fastest supercomputing site with 164K cores, a LINPACK performance of 0.46 pFLOP/s, and a 

)
11 

peak performance of 0.56 pFLOP/s. During the period from October 2011 through October 2013, Intrepid’s average job size was 9K 

cores, with its smallest job being 256 cores, and largest job size used all 164K cores. Although Intrepid is a somewhat less capable system than Pleiades, the utilization patterns are in stark contrast. Further, for both Mira and Intrepid, 

the overall utilization is still high, with Mira’s scheduled availability being utilized at 76% and Intrepid’s at 87%.4 A recent extreme example of capability computing using CFD is the 1.97M core simulation of shock interaction with isotropic turbulence (image shown) that was performed by combining the DOE’s Sequoia and Vulcan systems.5,6

Looking toward CFD in the 2030s and beyond, the need for improved physics-based modeling in 

CFD is driving increasingly expensive simulations that will only be possible by leveraging leadership class HPC systems. Without NASA’s leadership in the application of capability computing to 

CFD, the adoption of these technologies in the United States aerospace engineering industry will 

be hampered. 

1 http://www.top500.org/ 

2 http://www.nas.nasa.gov/hecc/resources/pleiades.html 

3 http://www.doeleadershipcomputing.org/incite-program/ 

4 Data courtesy of the Argonne Leadership Computing Facility at Argonne National Laboratory, which is supported by the Office of Science of the U.S. Department of 

Energy under contract DE-AC02-06CH11357. 

5 Bermejo-Moreno, I., Bodart, J., Larsson, J., Barney, B., Nichols, J., and Jones, S. "Solving the Compressible Navier-Stokes Equations on up to 1.97 Million Cores 

and 4.1 Trillion Grid Points." SC13, November 17-21 2013, Denver, CO, USA. 

6 Larsson, J., Bermejo-Moreno, I., and S. K. Lele. "Reynolds- and Mach-Number Effects in Canonical Shock-Turbulence Interaction." Journal of Fluid Mechanics, 

717:293–321, 2013. 

We envision the leading edge HPC system in 2030 will 

have a peak capability of about 30 exaFLOPS when based 

on the evolution of current technologies. To achieve this 

anticipated hardware performance, and the required flow 

solver software enhancements to enable effective CFD on 

2030 computing systems, a number of technology gaps and 

impediments must be overcome. 

1. Hardware system power consumption. Current stateof-the-art computing systems consume too much power 

to be scaled up substantially, utilize structural components that are too large, and do not provide the level of 

computational and communication speed necessary. 

Development of advanced HPC hardware technologies 

with a special focus on power consumption and error 

protections and recovery is needed. 

2. Higher levels of software extraction. The increased 

complexity of HPC exascale systems in 2030 will require higher levels of automation and the ability to hide 

this complexity from the subject matter experts. The 

whole software infrastructure stack does not scale to 

the level of complexity of future HPC systems and 

needs to be more resistant to errors. To overcome this 

gap, research into industrial strength implementations 

of the necessary middleware, especially operating systems, compilers, communication, and I/O libraries, as 

well as deployment and monitoring systems needs to 

continue. 

3. Advanced programming environments. Another 

critical component in the development of the full future 

HPC ecosystem is the development of basic, highly 

scalable and error resistant algorithms, decomposable 

software architectures, and programming environments 

that allow scientific subject matter experts to express 

algorithms at the appropriate level of abstraction. 

4. Robust CFD code scalability. As described earlier, an 

HPC system in 2030 will require tremendous levels of 

parallelization. Unfortunately, robust CFD flow solver 

scalability even on current multicore platforms is sorely lacking. Few applications can make efficient use of 

more than O(1,000) cores, although the largest machines today are available with O(1,000,000) cores.62

In contrast, 20 years ago, production CFD codes ran 

routinely on the largest available shared-memory vector machines. To address these challenges new, extremely parallel CFD algorithms that balance computing and communication need to be developed. Furthermore, there needs to be investment in the development of CFD codes built on highly optimized libraries 

and middleware. In contrast, current CFD codes and related processes are rather monolithic today, making it 

difficult to change algorithms or implementations. A 

future CFD code and surrounding processes should be 

modular, allowing replacement of components with 

new components developed in academia or from commercial vendors easily and transparently. Such a modular approach would also enable coupling of MDA/O 

processes. 

5. Lack of scalable CFD pre- and post-processing 

methods. Despite the deficiencies in current CFD 

solver scalability, the situation for the surrounding infrastructure of pre- and post-processing software is 

even worse. In order to streamline and accelerate the 

entire CFD workflow and design process, the development of basic scalable pre- and post-processing 

methods must be addressed. This includes geometry 

representation and mesh generation on the front end as 

well as visualization, database generation, and general 

knowledge extraction from large datasets on the back 

end. 
12 

6. Lack of access to HPC resources for code development. Another key issue is the lack of access to largescale HPC resources as an integral part of software development. Consistent and reliable access to leadingedge HPC hardware is critical for devising and testing 

new techniques that enable more advanced simulations, 

as well as for demonstrating the impact that CFD technology enhancements can have on aerospace product 

development programs.11, 39 Algorithmic choices and 

software implementation strategies are directly affected 

by the type of hardware made available during the software development process, and the stagnating scalability 

of current production CFD codes is at least partly attributable to the inability to test these codes consistently 

on large-scale HPC hardware. The resulting situation of 

scalability-limited simulation tools reduces demand for 

large-scale capability computing since few codes can 

take advantage of HPC hardware, while driving demand 

for throughput or capacity computing. Allocating a portion of HPC computing resources for highly scalable 

software development programs will be essential for 

pushing the boundaries of CFD simulation capabilities.45 

5.2 Unsteady Turbulent Flow Simulations Including Transition and Separation 

Perhaps the single, most critical area in CFD simulation 

capability that will remain a pacing item by 2030 in the 

analysis and design of aerospace systems is the ability to 

adequately predict viscous turbulent flows with possible 

boundary layer transition and flow separation present.23, 31, 

63, 64 While steady, fully turbulent attached flows can be 

predicted reasonably well with current RANS methods at 

all speed regimes,23, 65, 66 all types of separated flows are 

still difficult to predict. In particular, smooth body separation remains very hard to simulate accurately and efficiently 

for high-speed (buffet-limited) stall, low-speed high-lift, 

inlets at crosswind conditions, engine simulations and compressor stall, flows at the edges of the design envelope, and 

for maneuvering flight with moving control surfaces. In 

general, two critical components of flow physics need to be 

modeled accurately: the exact location of separation as controlled by boundary-layer physics and the feedback from 

the separated region to the boundary layer. 

Based on feedback from the CFD survey and the follow-up 

workshop held as part of this study, it is clear that the majority of the engineering and scientific community believes 

that RANS-based turbulence models, in conjunction with 

the expanded use of hybrid RANS-Large Eddy Simulation 

(LES) methods, will be the norm in 2030. This sentiment 

was confirmed from discussions at the workshop: all of the 

invited speakers in the session on turbulence predicted the 

continued use of RANS, including one and two-equation 

models, as opposed to the more complex Reynolds-Stress 

Transport models. They also predicted the extensive use of 

hybrid methods. However, LES-dominant methods for the 

range of engineering problems of interest (specifically for 

higher Reynolds numbers) will likely not be feasible based 

on current estimates of HPC computing performance in 

2030 using standard CFD approaches (see “Case Study 2: 

LES Cost Estimates and 2030 Outlook” below). 

In the area of viscous turbulent flows with transition and 

separation, a number of technology gaps and impediments 

must be overcome to accurately model these flows in the 

2030 timeframe. Specifically, they are: 

1. Lack of a theoretically based, hybrid RANS-LES 

turbulence simulation capability. Ideally, unsteady 

flow simulations using advanced turbulence models 

(e.g., DES, full LES) should be used to resolve the key 

turbulent length scales that drive development and propagation of flow separation. There has been progress in 

the representation of post-separation physics with the 

use of hybrid RANS-LES, or in general, turbulenceresolving methods (i.e., at least the part of the domain 

that is solved in LES mode).67, 68 In contrast, however, 

the prediction of pre-separation physics is still provided 

by RANS models, which have seen nearly stagnant development for 20 years.48 Unfortunately, hybrid methods 

are currently cost-prohibitive for routine use on realistic 

configurations at Reynolds numbers of interest in aerospace, at least in the thinner regions of the boundary layer such as near the wing attachment line. Another key 

impediment in fielding a robust hybrid RANS-LES capability is the changing nature of the interface between 

RANS and LES regions. For hybrid methods to be routinely used, a seamless, automatic RANS-to-LES transition in the boundary layer is urgently required.69 

2. Availability and convergence of complex turbulence 

models in practical codes. A recurring issue in using 

elaborate RANS models with second moment closures 

(e.g., Reynolds Stress Transport methods) for practical 

applications is both their availability in widely used flow 

solvers (e.g., FUN3D, OVERFLOW) and their notoriously poor convergence characteristics for flow simulation involving complex geometries and/or complex flow 

physics.70 The key impediments are the complexity of 

the models themselves manifesting in myriad variations, 

inadequate attention to numerics during design of the 

models, and the lack of powerful solution techniques in 

these codes that may be needed to solve the flow and 

turbulence model equations.71
13 

CASE STUDY 2: LES Cost Estimates and 2030 Outlook 

The predictions of when LES will be available in a reasonable turnaround time for engineering use have been performed by numerous 

researchers. Here, we focus on wall-modeled LES (WMLES) in which the anisotropic near-wall region is modeled in some manner such 

that the LES is responsible only for the larger, more isotropic outer flow. In 1979, Chapman estimated that such wall-modeled LES 

would be possible in the 1990s for practical aerodynamic applications.1 This clearly has not been realized in practice and one key factor 

in the optimistic predictions of Chapman was an underestimation of the computational work required for LES. Since that time, Spalart, et 

al. in 19972 and 20003 revised the computational cost estimates and predicted that full-wing LES would not be available for engineering 

use until 2045. Most recently, Choi and Moin4 revisited Chapman’s estimate applying the analysis of Spalart to show that the required 

resolution for wall-modeled LES in the turbulent portion of a boundary layer flow (i.e., after transition) scales asymptotically with Reynolds number, that is the number of grid points N ~ ReL (Chapman had estimated N ~ ReL

2/5). 

A potential concern is that these estimates ignore the cost of the laminar and transitional region of the boundary layer. In fact, because 

this region is significantly thinner than the turbulent boundary layer (even though it is generally a much smaller fraction of the chord), the 

computational cost may be non-negligible. To be precise, we follow Spalart, et .al. 1997 and count the number of cubes of volume 3  , 

where  is the boundary layer thickness. We consider both the laminar (including transition) and turbulent region of a boundary layer 

on a unit aspect ratio NACA 0012 wing. The flow is modeled using the 2D coupled integral boundary layer method of Drela5 with transition estimated using an eN method (Ncrit = 9). The table below shows that the number of cubes in the laminar region is 10 to 100 times 

larger than in the turbulent region. Thus, we conclude that a key issue in the application of WMLES will be the modeling of the laminar 

and transitional region. 

255606.004.ppt

Rec Nlam

cubes Nturbcubes Ncubes (Total)

1e6 1.1e6 1.3e4 1.1e6

1e7 1.1e7 1.5e5 1.1e7

1e8 9.1e7 3.1e6 9.4e7

We can estimate the performance of WMLES on HPC in 2030. We base this estimate on existing second-order accurate finite volume 

and finite difference discretizations with explicit time integration. While clearly other options exist, in particular higher-order methods, this 

combination is representative of the class of algorithms currently being applied throughout aerospace CFD on LES and DES simulations. Thus, we are making estimates based solely on how increased computational power will impact the ability to perform WMLES

simulations. Specifically, we make the following assumptions: 

 The mesh is an isotropic refinement of the boundary layer cubes with n points in each direction (and thus n3 unknowns in a single 

cube). In this example, we choose n=20. 

 The timestep of the explicit method is equal to  h / a min where h / n min   min and  a is the freestream speed of sound. 

 The number of floating point operations per timestep per point is Citer. In this example, we choose Citer=1250. 

 The time integration is performed over CT convective timescales. In this example, we choose CT =100. 

The table below shows the petaFLOP/s required to achieve a 24-hour turnaround for Mach 0.2 flow around a unit aspect-ratio geometry 

(estimates for high aspect ratio wings can be obtained by scaling by the desired aspect ratio). We note that the FLOP cost scales with 

approximately ReL

1.3, which is due to ~ReL for gridding requirements and ReL1/3 for timestep requirements. Estimates for wall-resolved 

LES4 show gridding requirements that scale with ReL

13/7 which gives FLOP costs scaling with ReL2.5. 255606.005.ppt

Rec Ndof Niter PFLOP/s

1e6 9.0e9 4.6e7 6

1e7 8.5e10 1.5e8 180

1e8 7.5e11 4.6e8 5,000

FLOP

5.2e20

1.6e22

4.3e23

We can then compare these estimates to existing HPC capability as well as estimated capability in 2030. At present, the world’s top 

HPC machine is Tianhe-2, a supercomputer developed by China’s National University of Defense Technology, with a theoretical peak 

performance of 55 PFLOP/s (and an actual achieved performance of 34 PFLOP/s on the Linpack benchmark). Thus, by today’s capability, wall-modeled LES is feasible in a 24-hour turnaround time at Reynolds number of about 1 million on unit-aspect ratio geometries using existing algorithms. Looking ahead to 2030, the leadership class HPC machine is estimated to have a theoretical peak performance 

of about 30 exaFLOP/s (see Appendix A). Thus, by 2030, we could expect to perform these types of calculations on the leadership HPC 

machine. 
14 

Additional conclusions based on these results are: 

 For the higher aspect ratios that are more relevant to external flows, the costs will be an order of magnitude larger and thus out of the 

reach of even 2030 leadership HPC machines at the high Reynolds numbers of interest. 

 At lower Reynolds numbers, the cost differences between wall-modeled and wall-resolved LES disappear. Thus, for lower Reynolds 

number applications, e.g., in some components of turbomachinery, wall-resolved LES is feasible on leadership class machines today.6

 As additional complexities are introduced, e.g., the full geometric complexity of a turbomachinery or a high-lift configuration, the cost will 

increase further. 

 The cost estimate assumes that the laminar and transition regions are simulated using the same resolution (per cube) as in the turbulent 

region, i.e., the transition process is simulated. If the transition process could instead be modeled so that the grid resolution was essentially that required for steady laminar boundaries, then the cost of the laminar and transition region would become negligible compared to 

the turbulent region and reduces the above cost estimates by a factor of 10 to 100. 

 The wall modeling for this type of LES is a current weakness that could limit the reliability of using this approach for separation prediction. 

 While these types of LES calculations may be feasible on leadership class HPC machines, engineering CFD calculations are not often 

pursued at this level of parallelism. Rather, engineering CFD calculations tend to be performed with 1,000s and rarely 10,000s of compute nodes. Thus, to realize these capabilities will require effort to exploit existing and future HPC performance. 

 The potential impact of algorithmic work could be significant. For example, a 10-fold improvement due to algorithmic performance (e.g., 

through adaptivity, or higher-order discretizations, or improved solution algorithms) could bring these 24-hour calculations down to a few 

hours. Further, this could relieve some of the pressure on wall modeling and transition modeling by facilitating increased grid resolution 

(or improved accuracy at less cost), and head toward wall-resolved LES. 

1. Chapman, D. R., “Computational Aerodynamics Development and Outlook,” AIAA J. 17, 1293 (1979) 

2. Spalart, P. R., Jou, W.-H., Strelets, M., & Allmaras, S. R., “Comments on the feasibility of LES for wings, and on a hybrid RANS/LES approach” (invited). First 

AFOSR Int. Conference on DNS/LES, Aug. 4-8, 1997, Ruston, Louisiana. (In “Advances in DNS/LES,” C. Liu & Z. Liu Eds., Greyden Press, Columbus, OH). 

3. Spalart, P. R., “Strategies for turbulence modeling and simulations,” Int. J. Heat Fluid Flow 21, 252-263., 2000. 

4. Choi, H., and Moin, P., “Grid-point requirements for large eddy simulation: Chapman’s estimates revisited,” Phys. Fluids 24, 011702 (2012) 

5. Mueller, T. J. (ed.), Low Reynolds Number Aerodynamics, Lecture Notes in Engineering, Volume 54, 1989, pp 1-12. 

6. Tucker, P. G., “Computation of unsteady turbomachinery flows: Part 2-LES and hybrids”, Progress in Aerospace Sciences. ISSN 0376-0421, 2011

3. Effects of grid resolution and solution scheme in assessing turbulence models. A key gap in the effectiveness of current and future turbulence models is the effect 

of grid resolution and solution scheme on both the accuracy and convergence properties of the models. Studies 

show that adequate grid resolution is required to capture 

the full range of turbulence structures in models ranging 

from simple eddy-viscosity formulations to full LES and 

DNS simulations.55 Additionally, choice of solution 

scheme may be important when using marginal grid resolution for complex geometries. Much work has been 

performed on building-block geometries,23,65 but realworld cases are now too complex to assess full grid convergence.56

4. Insufficient use of foundational validation/ calibration datasets to drive physics-based improvements to 

turbulence prediction. Key experimental datasets are 

critically important in the ongoing development and refinement of the full range of turbulence models from 

RANS to LES. Typical impediments include test cost, 

large number of cases needed, and instrumentation limitations. Moreover, many existing datasets are often not 

effectively exploited to use all available data in assessing 

and improving models. 

5. Insufficient use of real-world experiments to validate 

turbulence models. In addition to building-block experiments, more specific test data from complex, integrated 

flow fields using geometries that are more representative 

of complex aerospace systems is needed. Impediments 

include balancing test cost and model complexity, difficulty in designing experiments, geometry deviations, 

measurement detail, and accuracy of CFD. 

6. Robust transition prediction capability. Boundary 

layer transition is not well predicted (if at all) in CFD 

practice, impacting wind tunnel to flight scaling, laminar 

flow prediction and control, turbomachinery design, and 

hypersonic transition/heating analysis, among others. 

Transition modeling for lower Reynolds number applications is particularly lacking, with specific impact on 

high bypass ratio turbomachinery and for the lower 

Reynolds number vehicles being designed today. Currently, en

 methods are difficult to use. However, there 

have been some novel and promising developments in 

transition prediction methods (e.g., the Langtry-Menter 

correlation-based model),50 but these partial-differential 

equation (PDE) based methods (as opposed to en

 techniques) must be calibrated for a wide range of flow regimes and problems of interest, and should be viewed as 

in-development and somewhat risky. Still, these methods are being improved and are propagating into both 

government and commercial CFD codes72 even as they 

(currently) do not account for the cross-flow mode of 
15 

transition. Solid research is needed both on the PDE and 

e

n

 tracks, with emphasis on both accuracy and ease of 

coupling with RANS codes. 

7. Lack of explicit collaboration among turbulence 

researchers. There is a general lack of close coordination between turbulence modelers and researchers both 

in the aerospace field itself (scattered amongst academia, industry, and government), and between researchers 

in aerospace and related fields. In order to generate the 

new ideas necessary to address the key issues of flow 

separation and transition, it is imperative that a more 

concerted effort be undertaken to connect members of 

the aerospace turbulence community to others in 

weather prediction, bio-fluids, and hydrodynamic 

fields. 

5.3 Autonomous and Reliable CFD Simulation 

Today, most standard CFD analysis processes for the simulation of geometrically complex configurations are onerous, 

both in terms of cycle time and process robustness. Even 

for simpler configurations that are typically analyzed during 

the conceptual design phase, full automation is essential in 

order for a conceptual designer to effectively exploit the 

capacity of high performance computers and physics-based 

simulation tools. Based on feedback from the engineering 

and scientific communities as determined through our CFD 

Vision 2030 survey and workshop, the key issues related to 

CFD automation and reliability can be categorized into the 

broad areas of mesh generation and adaptivity, discretizations, solvers and numerics, and error control and uncertainty quantification. 

Mesh generation and adaptivity 

Today, the generation of suitable meshes for CFD simulations about complex configurations constitutes a principal 

bottleneck in the simulation workflow process. Often the 

mesh generation phase constitutes the dominant cost in 

terms of human intervention, and concerns about the cost 

and reliability of mesh generation were raised repeatedly in 

the survey and workshop. However, since a computational 

mesh is merely a means to enable the CFD simulation, ultimately the mesh generation process should be invisible to 

the CFD user or engineer. Given a suitable geometry representation and a desired level of solution accuracy, a fully 

automated meshing capability would construct a suitable 

mesh and adaptively refine this mesh throughout the solution process with minimal user intervention until the final 

accuracy levels are met. This process allows the user to 

focus on the final solution without concern for the construction and maintenance of the underlying mesh. Achieving 

this vision of fully automated meshing requires overcoming 

various important current impediments. 

1. Inadequate linkage with CAD. Configuration geometry definitions required by mesh generation software 

are generally provided by computer-aided design 

(CAD) packages. However, there is currently no single 

standard for representing surface or solid geometries 

within CAD tools, complicating efforts to fully automate the link between mesh generation and geometry 

definition. Furthermore, many existing CAD geometry 

definitions are poorly suited for CFD analyses, either 

due to insufficient accuracy (non water-tight geometries often adequate for manufacturing purposes), or 

due to excessive detail not essential for the CFD analysis. This results in the need to incorporate specialized 

post-processing tools such as shrink-wrapping in the 

former case, and/or de-featuring techniques in the latter 

case. At the same time, additional information such as 

slope and curvature or even higher surface derivatives 

may be required for the generation of curved mesh elements suitable for use with higher-order accurate CFD 

discretizations.73,74 Finally, for adaptive meshing purposes, tight coupling between the CFD software and 

geometry definition is required to enable low-overhead, 

on-demand, geometry surface information queries 

within the context of a massively parallel computing 

framework.75 

2. Poor mesh generation performance and robustness.

Significant human intervention is often required in the 

mesh generation process due to lack of robustness. This 

is evidenced by the inability of current mesh generation 

software to consistently produce valid high-quality 

meshes of the desired resolution about complex configurations on the first attempt. Additionally, many current 

mesh generation algorithms (e.g., advancing-front methods) do not scale appropriately on parallel computer architectures, and most mesh generation software is either 

run sequentially, or using a small number of computer 

cores or processors. On the other hand, CFD solver 

technology has demonstrated very good scaling on massively parallel machines,76-78 and is demanding ever 

larger meshes, which the mesh generation community is 

finding increasingly difficult to deliver due both to 

memory and time constraints using desktop commodity 

hardware. During the last decade or more, developments 

in mesh generation software came from third-party 

commercial vendors and NASA investment in this area 

has essentially evaporated. However, fundamental advances in computational geometry and other areas will 

be key to improving the reliability, robustness, and parallel scalability of mesh generation capabilities, particularly as larger simulations using finer meshes about more 

complex geometries are sought. Additionally, paradigm 

shifts in meshing technology (i.e., cut cell methods, 

strand grids, meshless methods) may lead to revolutionary advances in simulation capabilities.79-82 

Discretizations, Solvers, and Numerics 

The core of an autonomous and reliable CFD capability 

must rely on efficient and robust discretization and solution 
16 

strategies. Discretizations must be tolerant of localized poor 

mesh quality while at the same time be capable of delivering high accuracy at low cost. Solution techniques must be 

scalable, efficient, and robust enough to deliver converged 

solutions under all reasonable conditions with minimal user 

intervention. One of the principal concerns raised throughout our survey and workshop was the high level of expertise 

and human intervention often required for performing and 

understanding CFD analyses, with a consensus that a principal requirement for relieving this dependency will require 

added investment in basic numerical methods research. 

Current gaps and impediments with numerical methods 

include: 

1. Incomplete or inconsistent convergence behavior. 

Most current CFD codes are capable of producing fully 

converged solutions in a timely manner for a variety of 

simple flow problems. However, most often these same 

tools are less reliable when applied to more complex 

flow fields and geometries,56,85 and may fail, or require 

significant user intervention to obtain adequate results. 

There are many possible reasons for failure, ranging 

from poor grid quality to the inability of a single algorithm to handle singularities such as strong shocks, under-resolved features, or stiff chemically reacting terms. 

What is required is an automated capability that delivers 

CASE STUDY 3: Scalable Solver Development 

The development of optimal solvers has been central to the success of CFD methods since the early days of numerical simulation, for 

both steady-state and time-implicit problems. Optimal solvers are defined as methods that are capable of computing the solution to a 

problem with N unknowns in O(N) operations. Because the number of unknowns in industrial CFD problems is most often very large 

(106 < N < 109), optimal solvers offer the potential for orders of magnitude increase in solution efficiency compared to simple iterative 

solvers, which most often scale as O(N2) or higher. 

Multigrid methods constitute the most successful and widely used optimal solvers for CFD problems. These methods were developed 

for CFD applications at an early stage, with considerable NASA investment. In the late 1970s, joint NASA collaborative work with academic leaders in multigrid solver technology produced some of the first successful multigrid 

solvers for potential flow methods1, followed by efficient multigrid solvers for the Euler equations2, and the Navier-Stokes equations. The success was such that multigrid methods were implemented and used in virtually all 

important NASA CFD codes, including TLNS3D, CFL3D, OVERFLOW, and more recently FUN3D. Multigrid 

methods have become essential solver components in commercial production codes such as Fluent and 

STARCCM+, and have received particular attention within the DOE where they are used in various large-scale 

production codes. Despite their early success, many impediments remain for successfully extending these solvers to larger and more complex problems. While most early NASA investment focused on geometric multigrid for structured meshes, extending these solvers to complex geometry CFD problems or even abstract matrix inversion problems requires the development of algebraic multigrid methods (AMG). At the same time, improvements to current multigrid strategies are required if these methods are to 

scale effectively on emerging massively parallel HPC hardware. Although NASA investment in further research on multigrid methods 

has stalled since the early 1990s, considerable research has been directed toward developing more optimal AMG solvers designed for 

use on petascale and exascale hardware within the DOE. For example, the Scalable Linear Solver group at Lawrence Livermore National Laboratory has developed parallel AMG technology and related methods such as Smoothed Aggregation techniques that maintain 

optimal solver qualities while delivering vastly improved scalability on massively parallel machines. Current capabilities include the 

demonstration of the solution of a problem involving over 1012 degrees of freedom with good scalability on over 100,000 cores.3 Although these solvers are publicly available, they have not drawn the interest of the aerospace CFD community, and will likely require 

considerable investment to modify and extend to production aerospace CFD problems. 

Multigrid method developments are often reported at dedicated multigrid specialist conferences. For example, the first successful multigrid solution of the Euler equations was reported at the 1983 Copper Mountain Multigrid Methods conference.2 This conference series 

was traditionally well attended by NASA participants and, as recently as 1996, the conference proceedings were edited and published 

by NASA Langley4. However, during the last decade there has been virtually no NASA presence at these conferences. This has been 

accompanied by a significant decline of scalable solver papers published in AIAA venues, while NASA CFD codes have remained confined to the same multigrid technology that was developed in those early years. 

1. South, J. C. and Brandt, A., “Application of a Multi-level Grid Method to Transonic Flow Calculations,” in Transonic Flow Problems in Turbomachinery, (Adam, T.C. 

and Platzer, M.F. eds.) Hemisphere, Washington, pp 180-207, 1977 

2. Jameson, A., “Solution of the Euler Equations for Two Dimensional Transonic Flow by a Multigrid Method,” Proceedings of International Multigrid Conference, Copper Mountain, April 1983, Applied Mathematics and Computation, Vol. 13, 1983, pp. 327-356. 

3. Baker, A. H., Falgout, R. D., Kolev, Tz. V., and Yang, U. M., “Scaling Hypre’s Multigrid Solvers to 100,000 Cores,” in High Performance Scientific Computing: Algorithms and Applications, M. Berry, et al., eds., Springer (2012). LLNL-JRNL-479591. 

4. Melson, N. D., Manteuffel, T. A., McCormick, S. F., Douglas, C. C. (eds.), “Seventh Copper Mountain Conference on Multigrid Methods,” NASA CP 3339, September 1996. 
17 

hands-off solid convergence under all reasonable anticipated flow conditions with a high tolerance to mesh irregularities and small-scale unsteadiness. Reaching this 

goal necessarily will require improvements in both discretizations and solver technology,86 since inadequate 

discretizations can permit unrealizable solutions, while 

temperamental solvers may be unable to reach existing 

valid solutions. Although incremental improvements to 

existing algorithms will continue to improve overall capabilities, the development of novel robust numerical 

techniques such as monotone, positivity-preserving, 

and/or entropy-preserving schemes87,88 and their extension to complex problems of industrial relevance offers 

the possibility of radical advances in this area. 

2. Algorithm efficiency and suitability for emerging 

HPC. In previous decades, NASA has invested heavily 

in numerics and solver technology, and it is well documented that equivalent advances in numerical simulation capability have been enabled through the development of more efficient algorithms compared to advances in HPC hardware.1,16-18 However, during the last 

decade, algorithmic investment has been dramatically 

curtailed, with the result that the many flow solvers in 

use today were developed more than 20 years ago and 

are well known to be suboptimal. Because solver optimality is an asymptotic property, as larger simulations 

are attempted, the potential benefits of better solvers 

grow exponentially, possibly delivering orders of magnitude improvement by the exascale computing 

timeframe. At the same time, the drive to more complex flows (including more complex turbulence models, stiff chemically reacting terms, or other effects) 

and tightly coupled multidisciplinary problems will require the development of novel techniques that remain 

stable and efficient under all conditions. Finally, existing numerical techniques were never conceived with 

massive parallelism in mind, and are currently unable 

to capitalize on the emerging massively parallel and 

heterogeneous architectures that are becoming the 

mainstay of current and future HPC. In order to improve simulation capability and to effectively leverage 

new HPC hardware, foundational mathematical research will be required in highly scalable linear and 

nonlinear solvers not only for commonly used discretizations but also for alternative discretizations, such as 

higher-order techniques.89 Beyond potential advantages 

in improved accuracy per degree of freedom, higherorder methods may more effectively utilize new HPC 

hardware through increased levels of computation per 

degree of freedom. 

Error control and uncertainty quantification 

Errors in current CFD simulations are not well understood 

or well quantified, including errors due to spatial and temporal discretization, incomplete convergence, and the physical models and parameters they embody. The lack of error 

quantification raises the risk that engineering decisions are 

based on inaccurate and/or uncertain results. The Vision 

2030 survey highlighted the need for improvements in error 

quantification. Furthermore, in terms of reliable and automated CFD simulations, discretization error estimation is a 

key ingredient for the realization of a solution adaptive process. Current error control and uncertainty quantification 

gaps and impediments include: 

1. Limited use of existing error estimation and control 

methods. Significant progress has been made in the estimation and control of discretization errors, in particular in terms of output-based techniques.90-93 However, 

while these techniques were demonstrated by multiple 

groups for steady 2D RANS94 and 3D inviscid flows,83

the applications to 3D RANS and unsteady flows were 

limited, in particular for complex geometries. These 

more complex applications have been severely impeded by the inadequacies of 3D anisotropic and timedependent adaptive meshing, as well as by poor robustness of current discretization and solution algorithms (i.e., to be able to solve flow and adjoint equations on potentially poor quality meshes during the 

adaptive process). 

2. Inadequacy of current error estimation techniques. 

While discretization error estimation techniques for 

outputs have improved during the past 10 years, these 

techniques do have fundamental limitations that could 

influence their application to increasingly complex 

problems. In particular, output-based error estimation 

techniques are based on linearizations about existing 

(approximate) solutions and as a result can have significant error when the flows are under resolved (even in 

the case of a linear problem, the techniques generally 

only provide error estimates and are not bounds on the 

error). Furthermore, for unsteady, chaotic flows (which 

will be a key phenomenon of interest as turbulent DES 

and LES simulations increase in use moving forward) 

linearized analysis will produce error estimates that 

grow unbounded with time (due to the positive Lyapunov exponent for chaotic flows).95,96 In these situations, existing output-based methods will be swamped 

by numerical error, rendering the sensitivity information meaningless. This issue will affect not only error estimation but also design optimization moving 

forward. 

3. Limited use of uncertainty quantification. The consideration of uncertainty due to parametric variability as 

well as modeling error raises significant challenges. Variability and uncertainty of inputs (boundary and initial 

conditions, parameters, etc.) to fluid dynamic problems 

are largely unquantified. Even if estimates are available 

and/or assumed, the propagation of these uncertainties 

poses a significant challenge due to the inherent cost, the 

lack of automation and robustness of the solution process, and the poor utilization of high performance com-
18 

puting. Even more challenging is the quantification of 

modeling error. This will likely require significantly 

more expensive methods (e.g., based on Bayesian approaches).97 While uncertainty quantification is being 

investigated in the broad research community, most notably through DOE and NSF led programs,98 the engineering community, and the aerospace community in 

particular, have had minimal investments to address 

these issues. 

5.4 Knowledge Extraction and Visualization 

An integral part of effectively using the advanced CFD 

technology envisioned in 2030 is the way in which the very 

large amount of CFD-generated data can be harvested and 

utilized to improve the overall aerodynamic design and 

analysis process. The resulting utilization of this data would 

include insight into pertinent flow physics, use with aerodynamic or multidisciplinary optimization, and generation 

of effective databases for a myriad of purposes, including 

control law development, loads assessment, 

flight/performance simulation, etc. 

A number of technology gaps and impediments in the area 

of knowledge extraction for large-scale CFD databases and 

simulations must be overcome to efficiently analyze and 

utilize CFD simulations in the 2030 time frame. 

1. Effective use of a single, high-fidelity CFD simulation. As high-performance computing (HPC) systems 

become faster and more efficient, a single unsteady CFD 

simulation using more complicated physical models 

(e.g., combustion) to solve for the flow about a complete 

aerospace system (e.g., airplane with full engine simulation, space vehicle launch sequence, aircraft in maneuvering flight, etc.) using a much higher number of grid 

points (~10 to 100 billion) will become commonplace in 

the 2030 time frame. Effective use (visualization and insitu analysis) of these very large, single, high-fidelity 

CFD simulations will be paramount.99 Similarly, higherorder methods will likely increase in utilization during 

this time frame, although currently the ability to visualize results from higher order simulations is highly inadequate. Thus, software and hardware methods to handle 

data input/output (I/O), memory, and storage for these 

simulations (including higher-order methods) on emerging HPC systems must improve. Likewise, effective 

CFD visualization software algorithms and innovative 

information presentation (e.g., virtual reality) are also 

lacking. 

2. Real-time processing and display of many highfidelity CFD simulations. By the year 2030, HPC capabilities will allow for the rapid and systematic generation of thousands of CFD simulations for flow physics 

exploration, trend analysis, experimental test design, 

design space exploration, etc. The main goal, therefore, 

is to collect, synthesize, and interrogate this large array 

of computational data to make engineering decisions in 

real time.39 This is complicated by a lack of data standards which makes collection and analysis of results 

from different codes, researchers and organizations difficult, time consuming and prone to error. At the same 

time, there are no robust, effective techniques for distilling the important information contained in large collections of CFD simulation data into reduced-order 

models or meta-models that can be used for rapid predictive assessments of operational scenarios, such as 

the correlation of flow conditions with vehicle performance degradation or engine component failures, or 

assessments of engineering tradeoffs as required in typical design studies.100 

3. Merging of high fidelity CFD simulations with other 

aerodynamic data. With wind tunnel and flight-testing 

still expected to play a key role in the aerospace system 

design process, methods to merge and assimilate CFD 

and multidisciplinary simulation data with other multifidelity experimental/computational data sources to 

create an integrated database, including some measure 

of confidence level and/or uncertainty of all (or individual) portions of the database, are required. Currently, the merging of large amounts of experimental and 

variable fidelity computational data is mostly carried 

out through experience and intuition using fairly unsophisticated tools. Well founded mathematically and statistically based approaches are required for merging 

such data,101-103 for eliminating outlier numerical solutions, as well as experimental points, and for generally 

quantifying the level of uncertainties throughout the 

entire database in addition to at individual data 

points.104

5.5 Multidisciplinary/Multiphysics Simulations 

and Frameworks 

We also assume that CFD capabilities in 2030 will play a 

significant role in routine, multidisciplinary analysis 

(MDA) and optimization (MDAO) that will be typical of 

engineering and scientific practice. In fact, in 2030 many of 

the aerospace engineering problems of interest will be of a 

multidisciplinary nature and CFD will have to interface 

seamlessly with other high-fidelity analyses including 

acoustics, structures, heat transfer, reacting flow, radiation, 

dynamics and control, and even ablation and catalytic reactions in thermal protection systems. With increasingly 

available computer power and the need to simulate complete aerospace systems, multidisciplinary simulations will 

become the norm rather than the exception. However, effective multidisciplinary tools and processes are still in their 

infancy. 

Limitations on multidisciplinary analyses fall under various 

categories including the setup and execution of the analyses, the robustness of the solution procedures, the dearth 

of formal methodologies to guarantee the stability and accuracy of coupled high-fidelity simulations, and the lack of 
19 

existing standards for multidisciplinary coupling. The result 

tends to be one-off, laborious, and nonstandard interfaces 

with other disciplines with dubious accuracy and stability. 

Multidisciplinary optimizations inherit all of these limitations and suffer from additional ones of their own, including the inability to produce accurate discipline and systemlevel sensitivities, the lack of quantified uncertainties in the 

participating models, the lack of robustness in the systemlevel optimization procedures, as well as very slow turnaround times. 

The vision for 2030 MDA/O involves the seamless setup 

and routine execution of both multidisciplinary analyses 

and optimizations with 

 Rapid turnaround (hours for MDA and less than a day 

for MDO). 

 User-specified accuracy of coupled simulations. 

 Robustness of the solution methodology. 

 Ability to provide sensitivity and uncertainty information. 

 Effective leveraging of future HPC resources. 

For this vision to proceed forward, the development of multidisciplinary standards will be necessary, as well as the 

creation of coupling frameworks that facilitate the multidisciplinary interactions envisioned here. Moreover, key research challenges in multidisciplinary coupling, computation of system-level sensitivities, management of uncertainties in both the analyses and optimizations, hierarchical 

decomposition of the optimization problems, and both automation and standardization processes will need to be 

overcome. 

More specifically, a number of technology gaps and impediments must be tackled to enable truly multidisciplinary 

analyses and optimizations in the 2030 timeframe. In this 

report, we focus on the requirements that affect 2030 CFD. 

Although, by extension, we also discuss some more general 

gaps and impediments that are likely to affect our vision. 

1. Robustness and automation of CFD analyses in 

multidisciplinary environments. To ensure that 2030 

CFD can be an integral part of routine multidisciplinary, multiphysics simulations, the manpower cost required to set up and execute such calculations must be 

drastically reduced. Firstly, the setup of high-fidelity 

multidisciplinary analyses must be largely automated 

including all operations involving surface and volume 

grid transfers and interpolations, grid deformations 

and/or re-generation, information exchanges, and mappings to HPC environments. Secondly, the execution of 

multiphysics simulations that involve Vision 2030 

CFD must include appropriate measures to ensure the 

robustness of the solution procedure, protecting against 

coupled simulation failure and including the ondemand availability of all necessary modules in the 

CFD chain so that CFD failure modes are protected. 

Such automation and robustness characteristics provide 

the foundation for more complex problems that require 

the solution of multidisciplinary simulations.

2. The science of multidisciplinary coupling at high 

fidelity. Exchanges of information between Vision 

2030 CFD and other disciplinary solvers with which 

CFD will need to interact will require assurances of 

both accuracy and stability. Such properties often require the satisfaction of conservation principles to 

which close attention must be paid.105 Moreover, within the context of nonlinear phenomena and unsteady 

flows, the proper interfacing between CFD and other 

codes requires significant effort and can be hard to 

generalize. The development of libraries and procedures that enable high fidelity, accurate, and stable 

couplings, regardless of the mesh topologies and characteristic mesh sizes must be pursued. Such software 

may also need to be cognizant of the discretization details of the CFD solver. Ultimately, solvers using discretizations of a given accuracy (in space and in time), 

when coupled to other solvers, must ensure that the accuracy of the component solvers is preserved and that 

the coupling procedure does not give rise to numerical 

errors that may manifest themselves through solution 

instabilities.106

3. Availability of sensitivity information and propagation of uncertainties. Vision 2030 CFD is expected to 

interact with other solvers (for different disciplines) in 

multidisciplinary analyses and optimizations. In 2030, 

the state of the art is presumed to include the quantification of uncertainties (UQ), at the system level, arising from uncertainties in each of the participating disciplines. In order to facilitate both optimization and UQ 

at the system level, Vision 2030 CFD must be able to 

provide sensitivities of multiple derived quantities of 

interest with respect to large numbers of independent 

parameters at reasonable computational cost. Novel 

techniques for the propagation of uncertainties will 

need to be embedded into 2030 CFD for more comprehensive treatment of UQ problems. Moreover, the support for system-level sensitivity information and UQ 

will demand the availability of derivative and UQ information related to outputs of CFD that may be utilized by other solvers. Ensuring that these capabilities 

are present in our Vision 2030 CFD will permit advanced analyses, optimizations, and UQ to be carried 

out.

4. Standardization and coupling frameworks. Owing 

to the multitude of disciplinary solvers available for 

coupling with 2030 CFD, the uncertainty regarding the 

actual code structure, HPC solver architecture, and internal solution representation, it is fundamental to ensure that multidisciplinary simulation standards (such 

as the CGNS standard107 created for CFD) are created 

so that a variety of solvers can participate in multidisciplinary analyses and optimizations. Beyond the typi-
20 

cal codification of the inputs and outputs of a particular 

physical simulation, standards for MDAO may need to 

include sensitivities, uncertainties, and overall descriptions of the parameterization (possibly including the 

geometry itself) and the optimization problem. To enable tight coupling of diverse disciplines and codes, the 

data standards need to extend to include memory resident information and coding structures.57,59,60 

6 Technology Development Plan 

To achieve our vision of CFD in 2030 and directly address 

the key CFD technology shortcomings and impediments 

that currently limit the expanded use of CFD methods within the aerospace analysis and design process, a comprehensive CFD development plan has been developed and is presented in this section. In order to place future technology 

developments within the context of our Vision for 2030 

CFD, we first describe in more detail a number of Grand 

Challenge (GC) problems that embody the goals for CFD in 

2030. Next, a comprehensive roadmap that depicts key 

technology milestones and demonstrations needed to support the GC simulations is introduced and described. An 

integrated research plan is then proposed. Finally, an overall research strategy with specific recommendations for 

executing the plan to advance the state of the art in CFD 

simulation capability is provided. 

6.1 Grand Challenge Problems 

The intent of the GC problems is to drive the identification 

and solution of the critical CFD barriers that would lead to a 

desired revolutionary CFD capability. We purposely have 

chosen GC problems that are bold, recognizing that they may 

not be routinely achievable by 2030, but, if achieved, would 

represent critical step changes in engineering design capability. To this end, the GC cases are chosen to encompass the 

CFD capabilities required to design and analyze advanced air 

and space vehicles and systems in 2030, and represent important application areas of relevance to the various NASA 

aeronautics and space missions. Details on each of the four 

GC problems are given below. 

Grand Challenge Problem 1: 

LES of a powered aircraft configuration across the full 

flight envelope. This case focuses on the ability of CFD to 

simulate the flow about a complete aircraft geometry at the 

critical corners of the flight envelope including low-speed 

approach and takeoff conditions, transonic buffet, and possibly undergoing dynamic maneuvers, where aerodynamic 

performance is highly dependent on the prediction of turbulent flow phenomena such as smooth body separation 

and shock-boundary layer interaction. Clearly, HPC advances alone will not be sufficient to solve this GC problem and improvements in algorithmic technologies or other 

unforeseen developments will be needed to realize this 

goal. Progress toward this goal can be measured through 

the demonstration of effective hybrid RANS-LES and 

wall-modeled LES simulations with increasing degrees of 

modeled versus resolved near-wall structures with increasing geometric complexity. Fully optimized flow solvers 

running on exascale computing platforms will also be critical. 

Grand Challenge Problem 2: 

Off-design turbofan engine transient simulation. This 

case encompasses the time-dependent simulation of a 

complete engine including full-wheel rotating components, 

secondary flows, combustion chemistry, and conjugate 

heat transfer. This GC will enable virtual engine testing 

and off-design characterization including compressor stall 

and surge, combustion dynamics, turbine cooling, and engine noise assessment. Similar to GC 1, demonstration of 

advances in accurate prediction of separated flows, complex geometry, sliding and adaptive meshes, and nonlinear 

unsteady flow CFD technologies will be required to 

achieve this goal. In addition, advances in the computation 

of flows of widely varying time scales, and the predictive 

accuracy of combustion processes and thermal mixing, will 

be necessary. 

Grand Challenge Problem 3: 

MDAO of a highly flexible advanced aircraft configuration. The increased level of structural flexibility that is 

likely to be present in future commercial aircraft configurations (of the N+3 and N+4 types envisioned by NASA 

and its partners) dictates a system-level design that requires the tight coupling of aerodynamics, structures, and 

control systems into a complete aero-servo-elastic analysis 

and design capability. This GC problem focuses on the 

multidisciplinary analysis and optimization of such configurations including explicit aeroelastic constraints that may 

require a time-accurate CFD approach. In addition to the 

aero-servo-elastic coupling, this GC includes the integration of other disciplines (propulsion and acoustics) as well 

as a full mission profile. The ultimate goal is to demonstrate the ability (in both MDA and MDAO) to perform 

CFD-based system-level optimization of an advanced configuration that requires both steady and unsteady highfidelity models. 
21 

CASE STUDY 4: Impact of CFD Tool Development on NASA Science and Space Exploration Missions 

Traditionally, the development of physics-based simulation tools for aerospace vehicle analysis and design has been the responsibility 

of NASA’s Aeronautics Research Mission Directorate (ARMD), with an emphasis on solving ARMD’s aeronautics goals. However, 

NASA’s science and space exploration missions rely heavily on simulation tools. CFD has played a critical role in virtually all recent past 

and present NASA space vehicle programs, including Space Shuttle return to flight,1 entry-descent and landing (EDL) predictions for the 

entire series of Mars landings,2 support for the recent Constellation Program3 and, more recently, for the Multipurpose Crew Vehicle 

(MPCV) and the Space Launch System (SLS) programs. Throughout many of these efforts, limitations in numerical simulation tools for 

space vehicle design were uncovered, requiring expensive contingency planning. For example, the Ares I development, which employed 

a combination of wind-tunnel testing and CFD methods for aerodynamic database generation, found that CFD was often less reliable 

and more expensive than experimental testing, resulting in limited use of CFD principally in specific regions of the flight envelope where 

testing was not feasible.4 Similar conclusions were drawn by engineers developing the MPCV Orion aerodynamic database. 

In a recent yearly review of NASA’s Aerosciences State-of-the-Discipline, NASA’s technical fellow for Aerosciences has assessed the 

ability of the discipline to support NASA’s missions, and identified these top three technical challenges: 

 Prediction of unsteady separated flows 

 Aero-plume interaction prediction 

 Aerothermal predictions 

Accurate prediction of unsteady separated flow is critical in the design of launch vehicle systems, where buffet and aeroacoustic fluctuating pressures in the transonic regime during ascent can result in high vibrational environments. Currently, launch vehicle buffet environments 

are obtained almost exclusively through wind tunnel testing and correlation with empirical data 

at considerable expense and uncertainty, resulting in overly conservative structural mass and 

reduced payload to orbit. Advanced simulation techniques such as DES are beginning to be 

explored but have been found to be expensive and to require further refinement and validation. 

Similarly, quantifying the aeroacoustic environment in launch vehicle design due to separated 

flows and aero-plume interactions is an important consideration for flight qualification of vehicle 

electronic components and passenger safety. Previous vehicle programs such as Ares I have 

incurred considerable expense for the experimental determination of aeroacoustic environments, while investigations by NASA have determined that current CFD techniques are inadequate for the prediction of launch vehicle 

aeroacoustic environments.5 However, the largest payoff in launch vehicle design would come from the use of CFD as a dynamic flight 

simulation capability, rather than a static aerodynamic database generation tool, as is currently the case, although little effort is being 

targeted toward this area. Accurate prediction of separated flows is also an important consideration for spacecraft EDL, which is compounded by the need for accurate aerothermal predictions, which in turn are hindered by the need for reliable transition prediction and 

the inclusion of other multiphysics considerations such as radiation and ablator performance. Accurate simulation of the aero-plume interactions of the reaction-control systems for bluff body re-entry is another area where the development of accurate simulation capabilities could reduce cost and uncertainties associated with complex experimental campaigns. Finally, the design and validation of spacecraft decelerators, including high-speed parachutes and deployable decelerators would benefit enormously from the development of a 

reliable, nonempirical simulation capability, although this represents a complex nonlinear aero-structural problem with massive flow separation that is well beyond current capabilities. 

Clearly, there is a need for better simulation tools within NASA’s science and space exploration missions, as well as within aeronautics 

itself. Furthermore, many of the technological barriers are similar in both areas, such as the inability to accurately simulate separated 

flows and transition and the need to harness the latest HPC hardware, while other issues are more critical to the space mission such as 

aero-plume and aerothermal prediction capabilities. To overcome these deficiencies, increased coordination will be required between 

NASA’s science and space exploration programs, which are driving these requirements, and NASA aeronautics, where much of the expertise for simulation method development resides. In the place of the current approach, which relies on the periodic assessment of existing simulation tools, a longer term outlook that invests in new simulation capability development for specific space programmatic objectives must be adopted. 

1 Gomez, R. J., Aftosmis, M. J., Vicker, D., Meakin, R. L., Stuart, P. C., Rogers, S. E., Greathouse, J. S., Murman, S. M., Chan, W. M., Lee, D. E., Condon, G. L., and 

Crain, T., Columbia Accident Investigation Board (CAIB) Final Report. Vol. II, Appendix D.8. Government Printing Office, 2003. 

2 Edquist, K. T., Dyakonov, A. A., Wrightz, M. J., and Tang, C. Y., “Aerothermodynamic Design of the Mars Science Laboratory Backshell and Parachute Cone,” AIAA 

paper, 2009-4078. 

3 Abdol-Hamid, K. S., Ghaffari, F., and Parlette, E. B., “Overview of the Ares-I CFD Ascent Aerodynamic Data Development and Analysis based on USM3D,” AIAA 

paper, 2011-15, 49th AIAA Aerospace Sciences Meeting and Exhibit, Orlando, FL, January 2011. 

4 Malik, M. R. and Bushnell, D., (eds.), “Role of Computational Fluid Dynamics and Wind Tunnels in Aeronautics R&D,” NASA TP 2012-217602, September 2012. 

5 “Independent Assessment of External Pressure Field Predictions Supporting Constellation Program Aeroacoustics (ITAR),” NASA Engineering and Safety Center 

Report NESC-RP-07-040, September 2013. 
22 

Grand Challenge Problem 4: 

Probabilistic analysis of a powered space access configuration. The goal of this case is to provide a complete 

description of the aerothermodynamic performance, including reliable error estimates and quantified uncertainty 

with respect to operational, material, and atmospheric parameters, for a representative space vehicle throughout its 

flight envelope. This capability will enable reliability 

predictions and vehicle qualification in light of limited 

availability of ground-based test facilities. Demonstration 

of advances in combustion modeling, off-design performance, adaptive and dynamic overset meshing, unsteady 

flow, hypersonic flow, CFD reliability, and reliability and 

uncertainty quantification is required. 

Required research toward meeting these GCs is identified 

in six areas, namely HPC, physical modeling, numerical 

algorithms, geometry/grid generation, knowledge extraction, and MDAO, and is used to formulate the overall research plan. In order to evaluate the progress of each individual area of the research plan, technical milestones 

and demonstrations are formulated with notional target 

dates. While these provide a measure of progress in the 

individual technology roadmap domains, the capability of 

these combined technologies toward meeting the stated 

GC problems must also be evaluated periodically and 

used to prioritize research thrusts among the various 

technology areas. 

6.2 Technology Roadmap 

The CFD technology roadmap (presented in Figure 1) is a 

complete and concise view of the key research technologies 

and capabilities that must be developed, integrated into production CFD tools and processes, and transitioned to the aerospace CFD user community to achieve our vision of CFD in 

2030. The individual elements on the roadmap were identified based on the results of the CFD user survey, detailed 

technical discussions held during the Vision 2030 CFD 

workshop, and from interactions among our team members. 

Key technology milestones, proposed technology demonstrations, and critical decision gates are positioned along timelines, which extend to the year 2030. Separate timelines are 

identified for each of the major CFD technology elements 

that comprise the overall CFD process. The key milestones 

indicate important advances in CFD technologies or capabilities that are needed within each technology element. Technology demonstrations are identified to help verify and validate when technology advances are accomplished, as well as 

to validate advances toward the simulations of the GC problems identified above. The technology demonstration (TD) 

entries are linked by black lines in instances when a given 

TD can be used to assess CFD advances in multiple areas. 

Critical strategic decision gates are identified where appropriate to represent points in time where specific research, 

perhaps maturing along multiple development paths, is assessed to establish future viability and possible change in 

development and/or maturation strategy. Each individual 

timeline is colored by Technology Readiness Level (TRL) 

in three levels: low (red), medium (yellow), and high 

(green). The TRL scale is used to indicate the expected 

overall maturity level of each technology element at a specific point in time. In general, many of the critical CFD 

technologies are currently at a relatively low TRL level, but 

with proper research and development, mature to a high 

TRL level by 2030. Some of the CFD technologies must be 

sequentially developed and, therefore, it is not expected that 

all technologies will be at a high TRL in 2030. Specific 

details of the development plan for each technology element are given below. 

High Performance Computing (HPC). As mentioned previously, advances in HPC hardware systems and related 

computer software are critically important to the advancement of the state of the art in CFD simulation, particularly for 

high Reynolds turbulent flow simulations. Based on feedback 

from the user survey and from discussions during the CFD 

workshop, we envision HPC technology advancing along 

two separate paths. 

Ongoing development of exascale systems, as mentioned 

earlier, will continue through 2030, and represents the technology that will most likely provide the large increase in 

throughput for CFD simulation in the future.42,108 However, 

novel technologies, such as quantum computing or molecular computing, offer a true paradigm shift in computing 

potential and must be carefully considered at strategic 

points in the overall development plan, even though the 

technology is at a very low TRL level today. In order to 

properly address the HPC challenge, three specific thrusts 

must be supported. Firstly, current simulation software 

must be ported to evolving and emerging HPC architectures 

with a view toward efficiency and software maintainability. 

Secondly, investments must be made in the development of 

new algorithms, discretizations, and solvers that are well 

suited for the massive levels of parallelism and deep 

memory architectures anticipated in future HPC architectures.39,41 Finally, increased access to the latest large-scale 

computer hardware must be provided and maintained, not 

only for production runs, but also for algorithmic research 

and software development projects, which will be critical 

for the design and validation of new simulation tools and 

techniques.11, 45 We propose several key milestones that 

benchmark the advances that we seek: modification of 

NASA and related CFD codes to efficiently execute on hierarchical memory (GPU/co-processor) systems by 2020, 

initial evaluation of exascale performance on a representative CFD problem, and a demonstration of 30 exaFLOP 

performance for one or more of the proposed GC problems 

in the 2030 time frame. 
23 

Visualization

Unsteady, complex geometry, separated flow at flight Reynolds number (e.g., high lift)

2015 2020 2025 

HPC

CFD on Massively Parallel SystemsCFD on Revolutionary Systems(Quantum, Bio, etc.)TRL LOW

MEDIUMHIGH

PETASCALE

Demonstrate implementation of CFD 

algorithms for extreme parallelism in 

NASA CFD codes (e.g., FUN3D)

EX

Technology Milestone

Demonstrate efficiently scaled CFD simulation capability on an exascale system

30 

maneuv

simula

Physical Modeling

RANSHybrid RANS/LESLES

Improved RST models 

in CFD codes

Technology Demonstration

Algorithms

Convergence/RobustnessUncertainty Quantification (UQ)

Characterization of UQ in aerospace

Highly accurate RST models for flow separation

Large scale stocha

Knowledge Extraction

On demand analysis/visualization of a 10B point unsteady CFD simulation

MDAO

Define standard for coupling 

to other disciplines

High fidelity coupling 

techniques/frameworks

Incorporation of UQ for MDAO

UQ

Integrated transition 

prediction

Decision Gate

YES

NO

NO

Scalable optimal solvers

YES

Demonstrate solution of a NO

representative model problem

Robust CFD for complex MDAs

Automated robust solvers

Reliable error estimates in CFD codes

MDAO simulation of an entire 

aircraft (e.g., aero-acoustics)

On demand analysi100B point unstead

Creation of real-time multi-fidelity database: simulations plus test data with complete UQ 

WMLES/WRLES for complex 3D flows at appropriate Re

Integrated Databases

Simplified data representation

Geometry and Grid Generation

Fixed GridAdaptive Grid

Tighter CAD coupling

Large scale parallel mesh generation 

Production AMR in CFD codes

Uncertainty propagation capabilities in CFD

Grid convergence for a complete configuration

Multi-regime turbulence-chemistry interaction model

Chemical kinetics in LES

Chemical kinetics 

Combustion calculation speedup

Unsteady, 3D geom

(e.g., rotating turbomach

Figure 1. Technology Development Roadmap 
24 

Concurrently, we stress the importance of closely observing 

advances in revolutionary HPC technologies, such as superconducting logic, new memory technologies, alternatives to 

current Complementary Metal Oxide Semiconductor 

(CMOS) technologies with higher switching speeds and/or 

lower power consumption (specifically for graphene, carbon nanotubes, and similar developments), quantum computing and molecular or DNA computing. Because these 

technologies are in their infancy, we foresee decision gates 

in 2020, 2025, and 2030 to establish the ability of these 

systems to solve a relevant model problem61 (i.e., typical of 

a Poisson problem for PDE-based problems). Implicit in 

this strategy is the need to provide access to experimental 

hardware on a continual basis and to explore radical new 

approaches to devising CFD simulation capabilities. If, at 

any of these decision points, the technology clearly shows

its expected potential, we recommend increased investment 

to accelerate the use of these machines for CFD applications. 

A review of current HPC trends and a forecast of future 

capabilities are given in Appendix A. 

Physical Modeling. Advances in the physical modeling of 

turbulence for separated flows, transition, and combustion 

are critically needed to achieve the desired state of CFD in 

2030.1,23,24,31,39,63,64 For the advancement of turbulent flow 

simulation, we propose three separate tracks for research: 

RANS-based turbulence treatments; hybrid RANS/LES 

approaches where the entire boundary layer is resolved with 

RANS-based models, and the outer flow is resolved with 

LES models; and LES, including both Wall-Model 

(WMLES) and Wall-Resolved (WRLES). Details on each 

of the three development tracks and for transition and combustion modeling, are given below. Additionally, a longer 

term high-risk effort should investigate radically new approaches to physical modeling. 

RANS-based turbulence models continue to be the standard 

approach used to predict a wide range of flows for very complex configurations across virtually all aerospace product 

categories.23,30,56,66,85 As a result, the TRL level for these 

methods is high. They are easy to use, computationally efficient, and generally able to capture wall-bounded flows, 

flows with shear, flows with streamline curvature and rotation, and flows with mild separation. For these reasons, as 

well as the fact that RANS models will remain as an important component in hybrid RANS/LES methods, their use 

will continue through 2030. An advanced formulation of the 

RANS-based approach, where the eddy viscosity formulation 

is replaced with the direct modeling of the Reynolds stresses, 

known as the Reynolds Stress Transport (RST) method,109 in 

principle will be able to capture the onset and extent of flow 

separation for a wider range of flows.110 Currently, RST 

models lack robustness and are occasionally less accurate 

than standard RANS models. Solid research is needed in 

advancing RST models to production capability. To this end, 

we envision continued investment in RST models to 2020, 

including careful implementation, verification, and validation 

of the most promising variants of these models into research 

and production CFD codes, including hybrid RANS/LES 

codes. In the 2020 time frame, a comprehensive assessment 

of the ability of these models to predict flow separation 

would be enabled to determine whether or not further investment is warranted. 

Hybrid RANS/LES methods show perhaps the most promise 

in being able to capture more of the relevant flow physics for 

complex geometries at an increasingly reasonable computational cost.68,111 From the user survey, the majority of survey 

participants ranked the continued development of hybrid 

RANS/LES methods as the top priority in the area of turbulence modeling. However, as mentioned previously, several 

issues still exist. First, the prediction of any separation that is 

initiated in the boundary layer will still require improvements 

in RANS-based methods. Second, a seamless, automatic 

RANS-to-LES transition in the boundary layer is needed to 

enhance the robustness of these methods. Continued investment in hybrid RANS/LES methods to specifically address 

these two critical shortcomings will be required. Additionally, more effective discretizations and solvers designed specifically for LES type problems must be sought. When combined with advances in HPC hardware, these three developments will enable continued reduction in the RANS region as 

larger resolved LES regions become more feasible. It is fully 

anticipated that hybrid RANS/LES methods will become 

viable in production mode by the 2030 timeframe for problems typical of the proposed GCs. Ultimately, progress will 

be measured by the degree to which the RANS region can be 

minimized in these simulations and the added reliability they 

provide in predicting complex turbulent-separated flows. 

Application of LES to increasingly complex flows is a very 

active research area.112 At present, the TRL level of this technology is relatively low. As discussed in Case Study 2, cost 

estimates of WRLES show scaling with Reynolds number of 

about ReL

2.5 while WMLES is about ReL1.3, with the costs 

being the same at approximately ReL of 105

. For the typically 

higher Reynolds numbers and aspect ratios of interest to external aerodynamics, WRLES will be outside of a 24-hour 

turnaround even on 2030 HPC environments unless substantial advances are made in numerical algorithms. However, 

WRLES is potentially feasible in 2030 for lower Reynolds 

numbers and is a reasonable pursuit for many relevant aerospace applications including many components of typical 

aerospace turbomachinery.113 Further, the development of 

WRLES directly benefits WMLES in that the basic issues of 

improved HPC utilization and improved numerics are essentially the same for both. WMLES, however, requires additional development of the wall-modeling capability114 that is 

currently at a very low TRL. As such, we recommend investments in LES with emphasis on (1) improved utilization 

of HPC including developments of numerical algorithms that 

can more effectively utilize future HPC environments, and 
25 

(2) improved wall-modeling capability necessary for reliable 

WMLES. To this end, we envision waypoints to assess technology maturation: a technology demonstration of LES 

methods for complex flow physics at appropriate Reynolds 

numbers around 2020, and a GC problem involving complex 

geometry and complex flows with flow separation in 2030. 

Here, as for hybrid RANS/LES models, reductions in the 

wall modeled region ultimately leading to WRLES will be 

continuously sought through 2030 and beyond. 

Transition modeling is also a key area of investment, as an 

effective transition model would benefit RANS, hybrid 

RANS/LES, and LES (by relieving mesh requirements in the 

laminar and transition regions). Thus, an additional research 

thrust must be devoted toward the development of reliable 

and practical transition models that can be incorporated in the 

turbulence models being matured along each of the development tracks. The transition prediction method should be fully 

automatic, and be able to account for transition occurring 

from various mechanisms such as Tollmien–Schlichting 

waves, cross-flow instabilities, Görtler vortices, and nonlinear interactions associated with bypass transition. 

In the area of turbulent reactive flows, investment needs to 

continue toward the development of a validated, predictive, 

multiscale combustion modeling capability to optimize the 

design and operation of evolving fuels for advanced engines. 

The principal challenges are posed by the small length and 

time scales of the chemical reactions (compared to turbulent 

scales), the many chemical species involved in hydrocarbon 

combustion, and the coupled process of reaction and molecular diffusion in a turbulent flow field. Current combustion 

modeling strategies rely on developing models for distinct 

combustion regimes, such as non-premixed, premixed at thin 

reaction zone, and so forth. The predictive technology should 

be able to switch automatically from one regime to another, 

as these regimes co-exist within practical devices. Furthermore, research should continue into methods to accelerate the 

calculation of chemical kinetics so that the CFD solution 

progression is not limited by these stiff ordinary differential 

equations (ODEs). The deep research portfolios of DOE and 

the US Air Force can be leveraged to further these modeling 

needs. 

In addition to the above thrusts, a small portion of the research portfolio should be devoted to the investigation of 

radically novel approaches to physical modeling that may 

offer revolutionary changes in modeling capabilities. As an 

example, renormalization group theory115,116 has been proposed as a general framework for turbulence and other multiscale physical modeling, although revolutionary advances 

have not materialized specifically for turbulence modeling. 

Nevertheless, advances in multiscale modeling such as systematic upscaling (SU)106,117 offer the possibility for step 

changes in physical modeling capability, and should be pursued in a measured manner, similar to the proposed investments in radical HPC technologies.

Numerical Algorithms. The development of novel numerical algorithms will be critical to achieving the stated CFD 

2030 goals. Indeed, the proposed GCs are sufficiently ambitious that advances in HPC hardware alone during the next 

20 years will not be sufficient to achieve these goals. As 

demonstrated in Case Study 2, even for LES of relatively 

simple geometries, leadership class HPC hardware in 2030 

will be needed for 24-hour turnaround if existing algorithms 

are used. Thus, to tackle the proposed GCs, orders of magnitude improvement in simulation capabilities must be sought 

from advances in numerical algorithms.1,39 The focus of investment must be on discretizations and solvers that scale to 

massive levels of parallelism, that are well-suited for the 

high-latency, deep memory hierarchies anticipated in future 

HPC hardware, and that are robust and fault tolerant.41 A 

well balanced research program must provide for incremental 

advances of current techniques (e.g., extending the scalability 

of current CFD methods to the exascale level whenever possible), while at the same time investing in the fundamental 

areas of applied mathematics and computer science to develop new approaches with better asymptotic behavior for largescale problems and better suitability for emerging HPC 

hardware. 

Discretization techniques such as higher-order accurate 

methods offer the potential for better accuracy and scalability, although robustness and cost considerations remain.89

Investment must focus on removing these barriers in order to 

unlock the superior asymptotic properties of these methods, 

while at the same time pursuing evolutionary improvements 

in other areas such as low dissipation schemes,118-120 flux 

functions, and limiter formulations. Simultaneously, novel 

nontraditional approaches, such as Lattice-Boltzmann methods121,122 or other undeveloped schemes, should be investigated for special applications. Improved linear and nonlinear 

solvers must be developed, and here as well, the focus must 

be on highly scalable methods that are designed to be near 

optimal for the large-scale, time-implicit unsteady CFD and 

MDAO simulations anticipated in the future. These may include the extension of well-known matrix-based techniques, 

Krylov methods,123 highly parallel multigrid methods,124 or 

the development of completely novel approaches such as 

systematic upscaling methods.117 Furthermore, these methods 

must be extensible to tightly coupled multidisciplinary problems. Investment in discretizations and solvers must also 

consider the potential of these methods to operate on dynamically adapting meshes, to enable optimization procedures, 

and to incorporate advanced uncertainty quantification capabilities. In many cases, adjoint technology125,126 will be required from the outset for all of these capabilities, but the 

potential of other more advanced technologies such as second-order gradients (Hessians)127,128 should be investigated as 

well. Longer term, high-risk research should focus on the 

development of truly enabling technologies such as monotone or entropy stable schemes87,88 in combination with innovative solvers on large-scale HPC hardware. The technology 
26 

roadmap envisions the demonstration of improved robust and 

scalable solvers in the 2015-2017 timeframe, for both second-order and higher-order accurate methods. The demonstration of complete configuration-grid convergence technology in the 2020 time frame relies on the use of robust higherorder discretizations combined with improved scalable solvers and adaptive h-p refinement. Toward the 2030 time 

frame, it is anticipated that novel entropy stable formulations 

will begin to bear fruit for industrial simulations. 

With regard to uncertainty quantification, a new thrust in the 

area of probabilistic large-scale CFD for aerospace applications should be initiated. This program can build on the significant advances already made in this area by other government agencies,98 but provide the focus required for leveraging these technologies for aerospace applications.129,130 An 

initial thrust in this area should focus on enabling current 

aerospace CFD tools with well-known uncertainty quantification techniques, such as sensitivity analysis and propagation methods using adjoints and forward linearizations, nonintrusive polynomial chaos methods, and other reduced-order 

model formulations.131,132 Additionally, a concerted effort 

should be made to characterize important aerospace uncertainties and to make these available to the general research 

community for enabling relevant UQ research in these areas. 

Improved error estimation techniques must be investigated 

and developed, given the known deficiencies of current approaches (including adjoint methods). This will require a 

foundational program in the mathematics of error estimation 

and its application to CFD software. Finally, longer term 

research must focus on statistical approaches such as Bayesian techniques for quantifying more accurately modeling and 

other nonlinear error sources.97 The technology roadmap 

includes an early target date of 2015 for the characterization 

of typical aerospace uncertainties in order to stimulate work 

in this area. Improved error estimation techniques will be 

gradually brought into the simulation capabilities and the 

state of these estimates will be assessed in the 2018 time 

frame. Comprehensive uncertainty propagation techniques 

including discretization error, input and parameter uncertainties in production-level CFD codes should be targeted for 

2025, while the development of more sophisticated stochastic 

and Bayesian approaches will continue through the 2030 

timeframe. 

Geometry and Grid Generation. Substantial new investment in geometry and grid generation technology will be 

required in order to meet the Vision CFD 2030 goals. In general, this area has seen very little NASA investment during 

the last decade, although it remains one of the most important 

bottlenecks for large-scale complex simulations. Focused 

research programs in streamlined CAD access and interfacing, large-scale mesh generation, and automated optimal 

adaptive meshing techniques are required. These programs 

must concentrate on the particular aspects required to make 

mesh generation and adaptation less burdensome and, ultimately, invisible to the CFD process, while developing technologies that enable the capabilities that will be required by 

Vision 2030 CFD applications, namely very large scale 

(0(1012) mesh points) parallel mesh generation, curved mesh 

elements for higher order methods,73,74 highly scalable dynamic overset mesh technology,77,133 and in-situ anisotropic 

adaptive methods for time-dependent problems. It is important to realize that advances in these areas will require a 

mix of investments in incremental software development, 

combined with advances in fundamental areas such as computational geometry, possibly with smaller components devoted to high risk disruptive ideas such as anisotropic cut-cell 

meshes,80 strand mesh ideas,81 and even meshless methods.82

Additionally, because significant technology currently resides with commercial software vendors, particularly for 

CAD interfaces and access, involving these stakeholders in 

the appropriate focused research programs will be critical for 

long-term success. Innovative approaches for achieving such 

partnerships must be sought out, such as the formation of 

consortiums for the definition and adoption of standards or 

other potential issues such as large scale parallel licensing of 

commercial software. The technology development roadmap 

envisions the demonstration of tight CAD coupling and production adaptive mesh refinement (AMR) in the 2015-2017 

time frame, followed by maturation of large-scale parallel 

mesh generation in the 2020-2025 time frame, and leading 

ultimately to fully automated in-situ mesh generation and 

adaptive control for large-scale time-dependent problems by 

2030. 

Knowledge Extraction. Petascale and exascale simulations 

will generate vast amounts of data and various government 

agencies such as the NSF and DOE have instituted major 

programs in data-driven simulation research.134,135 In order to 

make effective use of large scale CFD and MDAO simulations in aerospace engineering, a thrust in data knowledge 

extraction should be initiated. Ideally, this should contain 

three components, a visualization component, a database 

management component, and a variable fidelity, data integration component. Methods to process and visualize very largescale unsteady CFD simulations in real time, including results from higher-order discretizations, are required to support the advanced CFD capabilities envisioned in 2030. Although many of the current efforts in maturing visualization 

technology are being led by commercial vendors who continue to supply enhanced capabilities in this area, more fundamental research to directly embed visualization capabilities 

into production CFD tools optimized for emerging HPC platforms is needed to achieve real-time processing.99 Moreover, 

the CFD capability in 2030 must provide the analyst with a 

more intuitive and natural interface into the flow solution to 

better understand complex flow physics and data trends and 

enable revolutionary capabilities such as computational steering, which could be used, as an example, for real-time virtual 

experiments or virtual flight simulation.136,137 Foreseeing the 

capability of generating large databases with increasing computational power, techniques for rapidly integrating these 
27 

databases, querying them in real time, and enhancing them 

on demand will be required, along with the ability to provide 

reliable error estimates or confidence levels throughout all 

regions of the database. 

Finally, integrating high fidelity simulation data with lower 

fidelity model data, as well as experimental data from wind 

tunnel tests, engine test rigs, or flight-test data will provide a 

powerful approach for reducing overall risk in aerospace 

system design.101 Techniques for building large-scale flexible 

databases are in their infancy, and range from simple software infrastructures that manage large numbers of simulation 

jobs to more sophisticated reduced-order models,138 surrogate 

models, and Kriging methods.102,103 The objective of a research thrust in this area should be to apply existing techniques to current CFD simulation capabilities at a large scale, 

while simultaneously performing foundational research in the 

development of better reduced-order models and variable 

fidelity models that are applicable to aerospace problems and 

can support embedded uncertainty quantification strategies. 

The technology roadmap envisions the demonstration of realtime analysis and visualization of a notional 1010-point unsteady CFD simulation in 2020, and a 1011-point simulation 

in 2025. These technology demonstrations would be an integral part of the GC problems designed to benchmark advances in other CFD areas. The development of reduced-order 

models and other variable fidelity models will entail longterm research and will likely remain an active research topic 

past the 2030 time frame. However, the technology roadmap 

envisions the periodic assessment of the state-of-the-art in 

these areas at 5 to 10 year intervals, with investment directed 

toward demonstrating promising approaches on large-scale 

aerospace applications. 

Multidisciplinary Design and Optimization. The ability to 

perform CFD-based multidisciplinary analysis (MDA) and 

analysis/optimization (MDAO) relies on the availability of 

future capabilities that need to be developed between now 

and 2030. Pervasive and seamless MDAs (that can be routinely exercised in industrial practice for configuration studies, e.g., full aero-thermo-elastic/aeroacoustic simulations of 

entire airframe/propulsion systems including shielding) will 

require the development of accepted standards and APIs for 

disciplinary information and the required multidisciplinary 

couplings (such as with acoustics, combustion, structures, 

heat transfer, radiation). A concerted effort is envisioned that 

results in a set of standards available to the community 

around 2016. In parallel with this effort, it will also be necessary to develop high-fidelity coupling techniques that guarantee the accuracy and stability of high fidelity, tightly coupled 

MDAs,106 while ensuring that the appropriate conservation 

principles are satisfied with errors below acceptable thresholds. This capability, together with the coupling software that 

includes such information transfers must be available around 

2018. Together, the standards and the coupling techniques/software would enable demonstrations of two-way 

coupled MDAs with the best and most robust existing CFD 

solvers of the time, and guaranteeing coupling fidelity by the 

year 2020. Such demonstrations can focus on multiple aerospace problems of interest, including aircraft aerostructural/aeroelastic analyses, aircraft aero-acoustics, rotorcraft aero-structural and aero-acoustic couplings, unsteady 

combustion, re-entry aerothermodynamics and material response, and the like. Initially, such routine MDAs would 

focus on portions of an entire vehicle (around 2020) and 

would transition to the treatment of the entire system around 

2025. A number of capabilities also must be developed in 

order to enable MDAO with and without the presence of 

uncertainties (robust and reliability-based design). A major 

research component that is likely to span a significant period 

(from 2015 to 2025) is the work needed to endow industrialstrength CFD solvers with both gradient calculation and uncertainty quantification capabilities for use in multidisciplinary optimization. Some of this work has been described in 

the “Numerical Algorithms” section. For the gradient/ sensitivity analysis capability, we envision that the CFD solver 

will be able to compute this information for full unsteady 

flows for the turbulence models available at the time. Finally, 

all these new capabilities must come together on a series of 

MDAO grand-challenge demonstrations in the 2030 

timeframe. 

7 Recommendations 

In order to effectively execute the CFD development plan 

described above and achieve the goals laid out in the vision 

of CFD in 2030, a comprehensive research strategy and set of 

recommendations are presented. This research strategy calls 

for the renewed preeminence of NASA in the area of computational sciences and aerodynamics, and calls for NASA to 

play a leading role in the pursuit of revolutionary simulationbased engineering.

Aerospace engineering has had a long history of developing 

technology that impacts product development well beyond 

the boundaries of aerospace systems. As such, NASA is a 

critical force in driving technology throughout aerospace 

engineering directly by fulfilling its charter to “preserve the 

role of the United States as a leader in aeronautical and 

space science technology.”

139 Computational methods are a 

key example of this broad impact, as NASA has historically 

been a leader in the development of structural finite-element 

methods, computational fluid dynamics, and applications of 

HPC to engineering simulations. The criticality of engineering-based simulation to the competitiveness of the United 

States and the lack of sustained federal support have been 

highlighted previously by the NSF37 and elsewhere.17,32

NASA’s effort must be targeted toward research and technology development that can make revolutionary impacts on 

simulation-based engineering in the aerospace sciences. In 

particular, the current state of CFD is such that small, incremental improvements in existing capability have not had 
28 

revolutionary effects. In an environment of constrained resources, this will require that NASA evaluate its activities 

with a critical eye toward supporting those efforts whose 

impact could be revolutionary. 

To ensure that the technology plan and roadmap are as effective as possible, we propose specific recommendations in 

three broad areas: enhancement of the current Revolutionary 

Computational Aerosciences (RCA) program, important programmatic considerations, and key strategic initiatives that 

taken together will help achieve the goals of our vision of 

CFD in 2030. 

7.1 Development of a Comprehensive Revolutionary Computational Aerosciences Program 

Recommendation 1: NASA should develop, fund and sustain 

a base research and technology (R&T) development program 

for simulation-based analysis and design technologies. 

Physics-based simulation is a crosscutting technology that 

impacts all of NASA aeronautics missions and vehicle classes, as evidenced by the common themes in the NAE Decadal survey report.12 In addition, technologies developed within NASA’s Aeronautics Research Mission Directorate impact 

many other aspects of the missions of various other NASA 

directorates. Yet, until recently, there has been no systematic 

program for developing simulation technologies, and all advances in simulation and CFD methods had to be justified by 

potential short-term impacts on one of the existing programs, 

or were done in response to critical simulation failures observed through the course of a program. This leads to the 

preference for small improvements to existing software, with 

the result that most current software is more than 20 years 

old, and the initiation of any new software project cannot be 

supported. Furthermore, investment in developing revolutionary simulation technologies is out of the question within 

such a program structure due to the long fruition time required and distant impact on existing programs. Yet without 

a focused base R&T development program, CFD will likely 

remain stagnant. Other international government agency 

aeronautic programs (such as DLR and ONERA) contain a 

base R&T component that is used to advance simulation 

technologies140,141 and certainly the new NASA Revolutionary Computational Aerosciences (RCA) program is a step in 

the right direction. However, NASA must ensure this program is strengthened, maintained, and expanded to cover 

investment in the critical elements required for advancing 

CFD and other physics-based simulation technologies as 

outlined in our research roadmap. 

An integrated research plan is required for the fulfillment of 

the technology development roadmap and eventual demonstration of the GC problems. At present, the current RCA 

program within the Aeronautical Sciences Project of the 

Fundamental Aeronautics Program (FAP) is too narrow in 

scope to address all the required technology areas in this report. Thus, we recommend broadening and enhancing the 

RCA program in several ways. The Aeronautical Sciences 

Project encompasses various subtopics including the RCA 

program, but also other areas such as materials, controls, 

combustion, innovative measurements, and MDAO. 

We recommend that all components of subtopics focused on 

computational simulation technologies be coordinated with 

the RCA program. For example, numerical simulation of 

combustion is an important technology that would be ill 

served by being isolated from the developments achieved 

under the RCA program. Thus, we suggest joint oversight of 

the numerical modeling aspects of combustion between the 

RCA program and the combustion program. Similarly, significant components of MDAO related to solver technology 

and interfacing CFD with other disciplines will benefit from 

close interaction with the RCA program. Next, we recommend that the RCA program be structured around the six 

technology areas that we have outlined in this report, namely 

HPC, Physical Modeling, Numerical Algorithms, Geometry/Grid Generation, Knowledge Extraction, and MDAO. 

Currently, the RCA program contains technology thrust areas 

specifically in Numerical Algorithms and Turbulence modeling. Thus, the recommended structure represents a logical 

extension of the current program, achieved by extending the 

turbulence modeling technical area to a physical modeling 

technical area (i.e., adding transition modeling and combustion modeling), coordinating the relevant MDAO thrusts 

within the broader Aerosciences program, and adding the 

other required technology areas. Additionally, collaboration 

in computational methods between RCA and the Controls 

and the Structure and Materials programs should be encouraged, while CFD validation thrusts can be expected to benefit 

from collaboration with the Innovative Measurements program. This new programmatic structure is illustrated in Figure 2. 

In the preceding section, each technical area is described in 

detail and the required research thrusts for advancing each 

area is provided. Naturally, individual research thrusts affect 

multiple technical areas, which in turn affect the ability to 

meet various milestones and progress toward the GC problems. However, for programmatic reasons it is desirable to 

have each individual research thrust reside within a single 

technology area. The success of this strategy relies on good 

communication and interaction between the different technology areas over the life of the program. A concise view of 

the proposed research program structure, including all technology areas and research thrusts is given in Figure 3. 
29 

The overall program goals are driven by the GC problems, 

which embody the vision of what CFD should be capable of 

achieving with balanced investment over the long term, and 

provide a means for maintaining program direction and 

measuring progress. While advances in all technology areas 

will be critical for achieving the GC problems, certain areas 

are described in less detail than others (e.g., knowledge extraction, combustion, MDAO), and this is partly due to the 

focus on CFD technology in the current report. As can be 

seen, the proposed research program contains a balanced mix 

of near-term and long-term research thrusts. The overall program is also highly multidisciplinary and draws on advances 

in disciplines at the intersection of aerospace engineering, 

physics of fluids, applied mathematics, computational geomAERONAUTICAL SCIENCES PROJECT

STRUCTURES AND

MATERIALS CONTROLS COMBUSTION INNOVATIVE

MEASUREMENTS MDAO

Newthrust

Shared investment and

technology collaboration

AERONAUTICS RESEARCH MISSION DIRECTORATE (ARMD)

SCIENCE MISSION

DIRECTORATE

(SMD)

HUMAN

EXPLORATION AND

OPERATIONS

DIRECTORATE

(HEO)

FUNDAMENTAL AERONAUTICS PROGRAM

Close coordination

HPC

Physical Modeling:

Turbulence

Transition

Combustion

Numerical Algorithms

Geometry/Grid

Knowledge Management

MDAO (Interfaces/coupling)

REVOLUTIONARY COMPUTATIONAL

AEROSCIENCES (RCA)

Figure 2. Proposed Enhanced Revolutionary Computational Sciences Program 

HPC

1. Increasing accessto leading‐edge HPC

hardware

2. Portingof current and future codesto

leading‐edge HPC

3. Radical emergingHPC technologies

PHYSICALMODELING

1. RANS turbulence modeling

2. Hybrid RANS‐LESmodeling

a. Improved RANS component

b. Seamlessinterface

3. LES (wall‐modeled andwall‐resolved)

4. Transition

5. Combustion

6. Radically newmodeling approaches

NUMERICAL ALGORITHMS

1. Advancesin current algorithmsfor HPC

2. Noveldiscretizations

a. Higher‐ordermethods

b. Low dissipation/dispersion schemes

c. Novelapproaches(foundational)

3. Solvers

a. Linear and non‐linearscalable solvers

b. EnhancementsforMDAOandUQ

4. UQ

a. Define aerospace uncertainties

b. Leverage known techniques

c. Improved errorestimation techniques

d. Statisticalapproaches

GEOMETRY AND GRID GENERATION

1. CADaccess and interfaces

2. Large scale parallel mesh generation

3. Adaptive mesh refinement

4. Curvedmesh elementsforhigher‐order

methods

KNOWLEDGEMANAGEMENT

1. Visualization

2. Data‐base management

3. Variable fidelitymodels

MDAO

1. Interfaces and standards

2. Accurate and stable coupling techniques

3. UQsupport and sensitivities(system‐

level)

Figure 3. Proposed New Revolutionary Computational Sciences (RCA) Program Structure 
30 

etry, computer science and statistics. Successful execution of 

the program will require devising appropriate mechanisms 

for leveraging expertise in these diverse fields. By its very 

nature, the formulation of a comprehensive research program 

of this type results in an exhaustive list of research thrusts 

that need to be addressed, and clearly prioritization of these 

individual thrusts must be performed within a limited budget 

environment. The prioritization of research thrusts and the 

prescription of funding levels must be an ongoing process 

and is certainly beyond the scope of this report. However, 

consistent mechanisms for making such decisions must be 

instituted. We propose the use of periodic workshops (e.g., at 

5-year intervals) convened to measure progress toward the 

GC problems, that can be used to identify the most critical 

technologies in need of investment, evaluate the success of 

previous investments, and prioritize future investments. 

7.2 Programmatic Considerations 

Recommendation 2: NASA should develop and maintain an 

integrated simulation and software development infrastructure to enable rapid CFD technology maturation. 

To reach the goals of CFD in 2030, research and technology 

development must effectively utilize and leverage in-house 

simulation expertise and capabilities with focused attention to 

HPC infrastructure, software development practices, interfaces, and standards. 

Maintain a World-Class In-House Simulation Capability.

To support broad advances in CFD technology, NASA’s 

simulation capability should be, in many aspects, superior to 

the capabilities that reside with academic and industrial partners and in the commercial software vendor arena. NASA’s 

in-house simulation code development is driven by the need 

to support NASA missions and must apply to all important 

application regimes of relevance to the NASA ARMD mission including fixed- and rotary-wing external aerodynamics, 

turbomachinery flows, combustion, aeroacoustics, and high 

speed flows, as well as applications of relevance to NASA’s 

science and space exploration missions. While NASA has 

excelled in many of these areas (notably fixed- and rotarywing external aerodynamics, and space vehicle entry, descent 

and landing [EDL]), there are other areas such as turbomachinery, combustion, and icing where it is believed that 

NASA’s capabilities are no longer on the cutting edge. Maintaining an in-house capability is crucial for understanding the 

principal technical issues and overcoming impediments, for 

investigating new techniques in a realistic setting, for supporting NASA’s own missions, and for engaging with other 

stakeholders. Whether technology transfer is ultimately 

achieved through the development of production level software that is adopted by industry, technology spin-offs to 

commercial software companies, or simply through realistic 

demonstrations on industrial problems with accompanying 

publications, has been the subject of much discussion for 

many years within NASA and the broader community, and 

remains beyond the scope of this report. However, what is 

evident is that without such an internal competence, NASA 

will be severely handicapped in any attempts to advance the 

state of the art in physics-based simulation technologies. Additionally, this recommendation is targeted to a broader audience at NASA than simply ARMD: given the deep reliance 

on simulation-based engineering for all mission directorates 

and the fact that an agency-wide coordination mechanism 

exists, efforts to develop world-class, in-house simulation 

capabilities should be cooperatively pursued. 

Streamline and Improve Software Development Processes. CFD software development at NASA has a checkered 

history. Many of the most successful codes in use today have 

their roots in the inspiration and the devotion of a single or 

small number of researchers. In some sense, this reflects one 

of the strengths of NASA’s workforce and work environment 

that, in the past, accorded significant scientific freedom. 

However, despite their successes, many of these codes are 

still maintained by a small number of developers who struggle to keep up with the increasing demands of bug fixes, application support, and documentation that comes with increased usage. 

Today, it is well recognized that software development must 

be a team effort due to increasingly complex software.41 43

While some NASA software projects (such as FUN3D) have 

successfully transitioned to a team effort model,142 there remains no formal structure for supporting software development issues such as regression testing, porting to emerging 

HPC architectures, interfacing with pre- and post-processing 

tools, general application support, and documentation. Most 

commercial software companies staff entire teams devoted to 

these types of activities, thus freeing the developers to pursue 

technology development and capability enhancements. CFD 

software efforts at DLR143,144 and ONERA,145,146 for instance, 

are known to provide continual support for dedicated software engineering tasks, while various US government projects such as the Department of Defense (DOD) Computational Research and Engineering Acquisition Tools and Environments – Air Vehicles (CREATE-AV) program have set 

up similar capabilities including an elaborate application 

support structure.60 Furthermore, if individual NASA codes 

are to be applied to diverse areas such as external aerodynamics, internal turbomachinery flows, combustion, LES and 

aeroacoustics, support of this type will be essential since no 

single individual can cover such a wide range of disciplines. 

While there are continual cost pressures to reduce the number 

of CFD codes being supported, mandatory use of a single 

code for all applications is overly constraining and even unfeasible in many cases for new technology development, 

since newly developed algorithms may be ill-suited for retrofitting into existing codes due to their data structures and 

inherent assumptions. Thus, the creation of a formal software 

support structure could provide relief and continuity to developers of established production codes while also facilitating and lowering the development costs of potentially prom-
31 

ising new software efforts designed either for research investigations or production CFD and MDAO. Moreover, this 

approach has the potential for cost savings due to reduction 

in duplication of efforts between individual software development projects. Ideally, these software components would 

be open-source and freely distributed within the United 

States and abroad. This would mark a significant departure 

from current NASA software practices, but could be 

achieved by isolating any sensitive capabilities in closed 

source software, as is regularly done at the US Department of 

Energy (DOE). 

Emphasize CFD standards and interfaces. Many of the 

impediments outlined in this report relate to the difficulty in 

accessing or exchanging information between various software components, such as CAD data for grid generation; 

AMR, post-processing data; or exchange of information between different components of a multidisciplinary problem. 

In many cases, the development of standardized interfaces 

can be used to greatly relieve these problems and facilitate 

further advances in CFD. As a government agency, NASA is 

uniquely positioned to spearhead the development and adoption of international standards and interfaces in various areas 

of CFD and MDAO. In particular, this is an activity that may 

not require significant funding in dollar terms, but will require identifying and organizing key stakeholders, developing a consensus among them, and continuing the advocacy 

and support of developed standards and interfaces. At the 

same time, it is important to note that frameworks and standardization can lead to significant constraints and may not be 

the best solution in all cases. Thus, a large part of such an 

effort must involve determining under what conditions standardization is appropriate, and then developing sufficiently 

flexible standards and building a consensus among all stakeholders. 

Recommendation 3: NASA should make available and utilize HPC systems for large-scale CFD development and testing. 

Access to leading-edge HPC hardware is critical for devising and testing new techniques that enable more advanced 

simulations,39,41 for demonstrating the impact that CFD 

technology enhancement can have on aerospace product 

development programs,11,45 and for addressing the GC problems defined previously. As described in Case Study 1, 

NASA’s HPC hardware is used primarily for throughput 

(capacity) computing rather than capability. Although 

hardware parallelism has increased dramatically during the 

last several decades, the average size of NASA CFD jobs 

remains well below 1,000 cores, even though the NASA 

Advanced Supercomputing (NAS) division flagship system 

contains over 160,000 CPU cores and is ranked 19th in the 

top 500 HPC installations worldwide.62 Other large HPC 

installations regularly allocate significant fractions of their 

resources toward enabling leading-edge petascale or higher 

simulation capabilities.45 Lack of access to large-scale HPC 

hardware on a regular and sustainable basis within NASA 

has led to stagnating simulation capabilities. To remedy this 

situation, NASA, and in particular the NASA Advanced Supercomputing (NAS) division, should make HPC available 

for large-scale runs for CFD research and technology development. Use of HPC for large-scale problems will drive demand by enabling testing of more sophisticated algorithms at 

scale, making users more experienced and codes more scalable since many issues are only uncovered through large-scale 

testing. However, this approach is complicated by the fact 

that ARMD only controls a fraction of NASA’s HPC resources. This will require advocating the benefits of largescale computing within NASA, either for modifying the current HPC usage paradigm, or for sharing resources between 

NASA directorates (e.g., Science Mission Directorate, Human Exploration and Operations) with an interest in more 

radical simulation capabilities. NASA ARMD must also leverage other national HPC facilities and enter into a discussion 

with the NSF, DOE and any other agencies for providing 

access to these systems on a regular basis for NASA objectives that overlap with these agency priorities147,148. Furthermore, NASA should remain at the forefront in new HPC 

technologies through the use of test platforms made available 

to the research community. The recently installed D-Wave 

Two quantum computer149 at NASA Ames is a good example 

of this, but it does not appear to be part of a concerted effort 

to track and test HPC developments. 

Recommendation 4: NASA should lead efforts to develop 

and execute integrated experimental testing and computational validation campaigns. 

During the past decade, workshops to assess CFD predictive 

capabilities have been effective in focusing attention in key 

areas important to the aerospace community such has drag 

prediction,23 high-lift prediction,56 and aeroelasticity,85 to 

name a few (see accompanying Case Study). In most cases, 

the workshops involve CFD simulation of challenging flow 

physics on realistic geometries. If available, experimental 

data is used to anchor the CFD predictions. However, with 

the exception of the Common Research Model (CRM) model 

development150 and transonic test campaign,151 workshops 

typically rely on pre-existing experimental datasets that often 

have an incomplete set of test data available, quality control 

issues, or a combination of both. Moreover, in many cases, 
32 

CASE STUDY 5: Community Verification and Validation Resources 

As numerical simulation capabilities become more complex, verification and validation (V&V) efforts become more important but also 

more difficult and time consuming. Verification is defined as the determination of whether a model is implemented correctly, whereas 

validation is defined as the determination of how well the model represents physical reality. One approach to reduce this burden and encourage higher V&V standards and usage is through the development of community resources for V&V. As a government agency, 

NASA is uniquely positioned to serve as the integrator and steward of such community resources. 

An excellent example of community V&V resources can be found in the NASA Turbulence Modeling Resource web site.1. The site is 

hosted by NASA, and the effort is guided by the Turbulence Model Benchmarking Working Group (TMBWG), a working group of the Fluid Dynamics Technical Committee of the AIAA, with contributions from NASA, academia, and industry. The objective of the site is to 

provide a central resource for turbulence model verification, which includes a precise definition of commonly used turbulence models including different model variants, and a set of verification test cases with supplied grids and sample results using different CFD codes, including grid convergence studies. By providing a sequence of progressively highly refined meshes, many of the verification test cases 

(principally in 2D) establish fully grid converged results for different CFD codes, providing a benchmark by which other codes can be 

measured to verify correct implementation of the model and consistency of the discretization. 

These are important prerequisites for applying implemented models to more complex cases 

with confidence. At present, the site provides descriptions for 11 turbulence models, and provides four verification test cases for which the most popular models have been tested with 

more than one CFD solver. The site also provides experimental data for a variety of 2D and 

3D test cases in order to facilitate model validation. 

During the last decade, the community workshop approach has emerged as a viable model for the validation of individual numerical 

simulation tools, as well as for the assessment of the entire state of the art in specific simulation capabilities. One of the original workshop series, the Drag Prediction Workshop (DPW), was initiated in 20012 and has since held five workshops.3 The first workshop in 

2001 was a grass-roots effort, which included substantial NASA participation, and focused mostly on comparison of CFD results for 

transport aircraft transonic cruise drag prediction, with secondary emphasis on comparison to available published experimental data. 

Over the years, the importance of high quality experimental data was increasingly recognized, leading to greater NASA involvement and 

investment, resulting in the design, fabrication and testing of the common research model (CRM), supported by NASA, including industry input, and conceived specifically for CFD validation purposes.4 Throughout this period, the DPW series has firmly established the importance of discretization error as a dominant error source (often larger than turbulence modeling error) for 

accurate CFD prediction of aircraft forces and moments. The DPW series has emphasized the need for careful grid convergence studies, resulting in the establishment and documentation of best practices for grid generation and grid convergence studies. Each individual workshop has provided a contemporary evaluation of 

the state of the art in CFD force and moment prediction, while the entire workshop series has enabled the 

assessment of continual improvements in the state of the art over more than 10 years. Reduced workshop 

result scatter can be correlated with evolving methodologies, increased grid sizes, and advancing computational power. The workshop series has also served to clearly identify the successes and deficiencies of current RANS methods, with particular emphasis on the rapid degradation of RANS predictive capabilities with 

increasing amounts of flow separation. Finally, the workshop series resulted in a large database of publicly 

available geometries, grids, and CFD results against which new software development programs can 

benchmark for more effective V&V. 

The success of the DPW has spawned other workshops in related areas, such as the High-Lift Prediction 

Workshop Series (HiLiftPW)5 and the Aeroelastic Prediction Workshop (AePW).6 A common feature of these 

workshop series, and other community V&V resources such as the NASA Turbulence modeling Resource 

web site, is that they combine the efforts of government, academia, and industry to promote advances in the 

state of the art, benefiting the community at large. However, in all cases, NASA involvement and investment 

has served as a key driver without which most of these endeavors would not be sustainable. 

1 http://turbmodels.larc.nasa.gov/

2 Levy, D. W., Zickuhr, T., Vassberg, J., Agrawal, S., Walls, R. A., Pirzadeh, S., and Hemsch, M. J., “Data Summary from First AIAA Computational Fluid Dynamics 

Drag Prediction Workshop,” AIAA Journal of Aircraft, 2003, Vol.4010.2514/1.1684 

3 http://aaac.larc.nasa.gov/tsab/cfdlarc/aiaa-dpw/

4 Vassberg, J., Dehaan, M., Rivers, M., and Wahls, R. A., “Development of a Common Research Model for Applied CFD Validation Studies,” 26th AIAA Applied Aerodynamics Conference, 2008, 10.2514/6.2008-6919 

5 http://hiliftpw.larc.nasa.gov/

6 https://c3.nasa.gov/dashlink/static/media/other/AEPW.htm
33 

the geometry definition of the tested configuration must be 

refurbished for CFD grid generation purposes. To help 

achieve the vision of CFD in 2030, an integrated approach 

involving well designed, ground-based (and perhaps flight152) 

experiments to provide high quality datasets directly coupled 

with CFD technology and application code verification and 

validation is required. This could be used in support of both 

CFD workshops, and the solution of GC problems, would 

help focus and solidify technology development in multiple 

areas, and establish best practices. Moreover, with physicsbased computational modeling continuing to expand, the 

need for systematic numerical validation test datasets and an 

effective mechanism to disseminate the results of the validation results are becoming paramount. NASA has both a full 

range of experimental test facilities in which to collect highquality data, as well as the computational tools and processes 

in which to benchmark CFD capabilities. For this reason, 

NASA should pursue a leadership role in developing complementary experimental and computational datasets to help 

guide CFD technology development. 

7.3 Strategic Considerations 

Recommendation 5: NASA should develop, foster, and leverage improved collaborations with key research partners 

and industrial stakeholders across disciplines within the 

broader scientific and engineering communities. 

Leverage other government agencies and stakeholders 

(US and foreign) outside of the aerospace field. Currently,

NASA ARMD’s interaction with other government entities is 

almost exclusively focused on agencies that have a major 

stake in the national aeronautics enterprise such as the Federal Aviation Administration (FAA), United Stated Air Force 

(USAF), and others. However, in the last decade, computational science has had important visibility at the national level, through various competitiveness thrusts,17,32 and has become an important focus for various agencies such as the 

DOE, NSF and the National Institute of Standards and Technology (NIST).153 Therefore, it is natural for NASA ARMD, 

which performs the bulk of the R&T in computational science for the agency, to seek out and establish meaningful 

collaborations with these traditionally non-aerospace focused 

agencies. However, such collaborations have been sorely 

lacking. For example, various multi-agency studies and white 

papers are frequently published on the topic of exascale 

computing,41,42,108 but surprisingly NASA has not been a participant in these multiagency discussions. With its limited 

budget, and dim prospects for improved research budgets, 

NASA ARMD cannot afford to “go it alone” and hope to 

make substantial progress in the important areas of computational science and simulation technology that are so important to advancing the agency’s mission in various directorates. Creative strategies must be devised to leverage funding and resources with other stakeholders with similar objectives, because the current approach has been shown to produce a stagnating capability in the environment of shrinking 

budgets during the last decade. These creative strategies can 

involve a wide range of partners from different directorates 

within the agency, such as Space Exploration and Science, to 

other agencies such as NSF and DOE, and in terms of hardware, software, and research results. As an example, the lack 

of access to HPC for NASA researchers could be addressed 

through a potential collaboration with DOE to obtain guaranteed slices of time on their leadership class machines through 

a formal program that could be negotiated at an interagency 

level, for example through the Networking and Information 

Technology Research and Development (NITRD) Program.147,148 In addition, many of the DOE- and DODsponsored advances in HPC were derived from investments 

in fundamental research that could be effectively leveraged 

by more direct NASA participation in the setup, running, and 

partial sponsoring of these efforts. Finally, Memorandums Of 

Understanding (MOUs) and other vehicles for interacting 

with foreign government agencies should be considered 

whenever possible. 

Improve collaboration with industry. NASA has been at 

the forefront of CFD technology for decades and was responsible for introducing much of the CFD technology used in 

industry today. At the same time, in collaboration with universities, industry has addressed additional CFD technology 

needs that are unique and essential to their business success. These include increased emphasis in the areas of physics-based modeling, rapid complex geometry and grid capabilities, managing the generation of CFD-based aerodynamic 

design matrices, improving accuracy and robustness, and 

integrating CFD databases with experimental data and other 

disciplines. The result has been a substantial reduction in 

physical testing but not uniformly across all products or flow 

regimes. Continued advances are required to address fullflight envelope predictions and propulsion system operating 

conditions, reduce design cost and cycle time, reduce ground 

and flight-testing, and enable product certification through 

analysis. Accelerated maturation of CFD technologies for all 

aerospace applications (e.g., external aerodynamics, turbomachinery, space) could be better achieved with expanded 

three-way collaboration between industry, NASA, and academia, beyond the current collaborations in physical testing 

at NASA facilities and research through NASA Research 

Announcements (NRAs). While industry is in a unique position to provide requirements and assess the value and impact 

of various CFD technologies on the aerospace industry, 

NASA is best positioned to coordinate and advance CFD 

technologies required for maintaining competitiveness and 

leadership. As mentioned above, many of these technologies 

require substantial advances in physical modeling (e.g., turbulence, transition, and combustion) and numerics (e.g., stability, accuracy, uncertainty quantification, gradient estimation, adjoint methods). These are traditional NASA strengths 

and should be re-emphasized. Further, NASA is also in a 

unique position to coordinate the definition of standards for 
34 

data, codes, and databases that would enable more rapid generation of next generation tools, and interfaces to industrial 

scale CFD applications. Similarly, critical areas that have 

mostly been left to industry (e.g., complex geometry representations, grid generation and 3D visualization) could also 

benefit from a renewed focus by NASA, perhaps in a closer 

partnership with both the aerospace industry and other industries that are similarly challenged, such as the automotive 

industry. Finally, we advocate the creation of a NASAIndustry Computational Science (CS) leadership team, which 

will be tasked with the mission of identifying joint CS projects oriented toward addressing the four GC problems presented in Section 6. We believe that projects with 3-year cycles accompanied by gate reviews from independent parties 

would facilitate and ensure maturation and transition of relevant technology to industry. 

Emphasize basic funding in applied math and computer 

science. In order to advance the state-of-the-art of CFD, advances must also be sought in related disciplines such as applied mathematics and computer science. We have referred to 

these throughout the report, invoking such areas as computational geometry for grid generation, applied mathematics for 

linear and nonlinear solver development, and computer science issues related to HPC. The specific areas of CFD, as 

well as the broader area of MDAO, are components of the 

general field of computational science. CFD lies at the intersection of applied math, computer science, and an application 

science area (in this case, aerodynamics), or more broadly, 

aerospace engineering.1,39 It is notable that at other government agencies, such as the NSF, a significant portion of funding for computational fluid dynamics comes from the mathematical and physical sciences program, while numerical 

solver groups at various DOE labs are staffed largely by scientists with degrees in applied math and/or computer science. 

The aerospace CFD and MDAO community is notoriously 

insular, with most researchers having an aerospace engineering background, publishing in AIAA or similar venues, and 

with scant presence in regular computational science meetings hosted by the Society for Industrial and Applied Mathematics (SIAM), the Institute of Electrical and Electronics 

CASE STUDY 6: Sponsored Research Institutes 

Currently NASA relies on a mix of internal development and external funding with academic and industrial partners through NASA Research Announcements (NRA) to advance its research goals. However, additional mechanisms must be sought to more fully engage the 

broader scientific community especially for computational science problems, which are both crosscutting and multidisciplinary. Sponsored research institutes have been used in many areas of science and engineering to further such goals. These institutes can take on 

various forms and funding models, ranging from fully self-supporting autonomous institutes such as the Southwest Research Institute 

(SWRI),1 university-based institutes, multi-stakeholder institutes, and government-agency based institutes. The nature, size, and funding 

model of these institutes must be considered based on the objectives of the sponsoring agency or stakeholders. 

The objective of a computational science based institute for NASA aeronautics would be to provide a centralized focal point for the development of crosscutting disciplines, to engage the broader scientific community, and to execute a long-term research strategy with sufficient autonomy to be free of NASA mission directorate short-term concerns. Under these conditions, the self-supporting research institute model such as SWRI is not appropriate due to the short-term pressures to continually raise research funding, and the difficulties in 

maintaining agency-related focus, given the diverse and changing composition of a competitively 

funded research portfolio. University-based institutes have been used successfully by a variety of 

funding agencies, and are the preferred mechanism for agencies with no internal facilities of their 

own, such as the National Science Foundation (NSF). During the last two decades, the NSF has 

set up a number of High Performance Computing (HPC) centers at universities across the United 

States, as well as various scientific institutes such as the Institute for Mathematics and its Applications (IMA) at the University of Minnesota.2 Mission agencies such as the DOE and NASA have 

also followed this model occasionally, for example through support for the previous DOE ASCI 

centers, NASA’s previous support of the CTR at Stanford University,3 and current DOE support 

for the PSAAP centers.4 Although many of these institutes have been highly successful, such a 

model may not be optimal for the considered objectives, since focused investment at specific universities is not an ideal mechanism for 

engaging the broader community, while at the same time geographical separation between sponsor and university can be a detriment to 

collaboration. 

A number of multi-stakeholder and agency co-located research institutes with aerospace-focused computational science objectives were 

used with generally favorable outcomes. CERFACS,5 located in Toulouse, France, is a research organization that aims to develop advanced methods for the numerical simulation of a wide range of large scientific and technological problems. CERFACS is organized as a 

private entity with shareholders, which include government agencies ONERA, CNES, Meteo France, and corporate sponsors EADS, 

SAFRAN, TOTAL, and Electricite de France (EDF). The shareholders fund the majority of research performed at CERFACS and, as a 

result, jointly own research results and intellectual property. The institute employs approximately 150 people, of which 130 are technical 

staff including physicists, applied mathematicians, numerical analysts, and software engineers. The institute is organized around inter-
35 

disciplinary teams that focus on the core fundamental area of numerical methods for parallel computing, combined with more applied focus areas in aerodynamics, gas turbines, combustion, climate, environmental impact, data assimilation, electromagnetism and acoustics 

and multidisciplinary code coupling. The CERFACS model is interesting because it brings together common computational science 

problems from different areas such as aeronautics, space, weather/climate modeling, and combustion, and includes combined government-industrial sponsorship. 

The C2A2S2E institute6 at DLR in Braunschweig Germany provides a model that is more focused on the development of computational 

science for specific aeronautics applications. The institute is jointly funded by DLR, Airbus, and the German State of Lower Saxony 

(Niedersachsen). The objective of the institute is to be an “interdisciplinary center of excellence in numerical aircraft simulations.” The 

institute was conceived as a major new aerospace simulation center under the DLR Institute of Aerodynamics and Flow Technology in 

Braunschweig, with the objective of providing a campus-like environment that brings together world-renowned experts and guest scientists to stimulate top-level research in the field of numerical simulation. Another function of the institute is to provide high-end computer 

simulation and visualization hardware and capabilities. C2A2S2E employs approximately 50 technical staff with expertise in applied 

mathematics, computer science, and aerospace engineering. 

In past years, NASA has used field-center co-located institutes such as ICASE at NASA Langley, ICOMP at NASA Glenn, and RIACS at 

NASA Ames as vehicles for long-term research and to better engage the broader scientific community. Arguably, the most successful of 

these was ICASE, which was created in 1972 and was supported for 30 years. The goal of ICASE was to perform long-term research in 

computational science and broadly related fields that was relevant to NASA’s aeronautics mission. The institute was rather small, with 

an average fluctuating total of 30 people of which approximately 25 were researchers, and with a robust visitor program of 50 to 70 people per year. Institute funding consisted of a mix of long-term core and short-term task funding from NASA, in approximately a 60/40 ratio, with a total budget of about $2M in the 1990s. While task funding was obtained directly from the supporting NASA center (Langley), 

experience had shown that it was important for the core funding to be obtained from NASA Headquarters directly, in order to shield the 

institute from the shorter term pressures and objectives of the supporting NASA center. A key to success was to be aware of long-term 

NASA goals, but also to acquire in-depth knowledge of broader interdisciplinary research performed at other research centers and universities both within the United States and internationally. A central purpose of the visitor program was to keep abreast of emergent 

technologies that the institute should be investing in to meet NASA’s long-term needs. Although shorter term in nature, task funding provided critical mass for the institute, lowering administrative costs, while at the same time tying the institute more closely to the needs of 

the NASA center, and thus enabling a better long-term vision. However, pressure to grow the institute through increased task funding 

needed to be resisted for the institute to retain its long-term focus. The institute was structured as a private nonprofit entity, managed by 

an outside umbrella organization. 

The above examples illustrate how differently structured research institutes can be used to achieve multidisciplinary and longer term research goals. In most cases, it is not the direct level of funding that determines the success of the institute; rather, it is the establishment 

of a structure that enables engagement of the broader scientific community and provides a long-term focus aligned with the sponsoring 

agency or stakeholder goals, while shielding the institute from shorter term pressures and objectives. 

1 http://www.swri.org/

2 http://www.ima.umn.edu/

3 http://nnsa.energy.gov/aboutus/ourprograms/defenseprograms/futurescienceandtechnologyprograms/asc/univpartnerships/psaap

4 http://ctr.stanford.edu/

5 http://www.cerfacs.fr/

6 http://www.dlr.de/as/en/desktopdefault.aspx/tabid-4083/6455_read-9239/

 Engineers (IEEE), and the Association for Computing Machinery (ACM). This trend can be noted as well in the various survey reports compiled for the national aerospace enterprise, such as the NAE decadal surveys12 and the National 

Aerospace R&D plans,13 which repeatedly refer to specific 

aerospace capabilities that must be developed through numerical simulation, without acknowledging the role developments in other related fundamental disciplines play in 

meeting these objectives. This should be contrasted with numerous reports issued by the DOE and NSF and other computational science-based studies that emphasize the needed 

investment in areas at the intersection of applied math, computational science and application science disciplines.16,18,37,106 An essential component for advancing stateof-the-art CFD will require that the research portfolio be expanded beyond pure aeronautics and fluid mechanics disciplines into these related fundamental areas. However, given 

its limited budget, NASA ARMD can ill afford to start new 

programs in these areas. Rather, the course of action should 

focus on specific areas with potentially high payoff that are 

unique to the NASA mission, as well as increased leveraging 

of ongoing activities within other government programs in 

the United States and abroad. At a minimum, NASA should 

establish a presence at the important computational science 

meetings hosted by SIAM, IEEE, and ACM to keep abreast 

of developments in these areas. 

Develop and foster collaborations with other disciplines 

through the creation of research institutes. As mentioned 

above, investments in applied math and computer science 

will be critical for achieving specific advances in CFD. 

Likewise, advances in MDAO will require investments in 
36 

key disciplines outside of traditional aerodynamics. However, the current makeup of NASA and the broader aerospace 

community is such that it will be difficult to obtain the required multidisciplinary expertise from within. Furthermore, 

it will likely be difficult to ensure relevance of investments in 

these more distantly related fields for maximum impact in 

aeronautics. 

In general, NASA relies on a mix of internal development 

and external funding of academia and industry through 

NASA Research Announcements (NRAs). However, other 

mechanisms are needed to engage scientists in other related 

disciplines. In the past, NASA relied on semi-academic institutes such as the Institute for Computer Applications in Science and Engineering (ICASE), the Institute for Computational Mechanics in Propulsion (ICOMP), the Research Institute for Advanced Computer Science (RIACS) set up at various NASA centers, and the Center for Turbulence Research 

(CTR) at Stanford University, to foster collaboration in specific, related disciplines and to engage the broader national 

and international scientific community in problems of relevance to the NASA aeronautics mission. During the last decade, larger institutes such as the National Institute of Aerospace (NIA) and the Ohio Aerospace Institute (OAI) were 

created and absorbed some of these functions. However, 

these institutes, which serve many purposes, are not devoted 

to specifically advance computational science issues and 

were not conceived to focus principally on NASA’s longer 

term requirements, (although they could be modified to include such aspects). It is noteworthy that the small, semiacademic institute model has been replicated at various other 

US national labs, such as the Center for Nonlinear Studies 

(CNLS) at Los Alamos National Laboratory (LANL) and the 

Institute for Scientific Computing Research (ISCR) at Lawrence Livermore National Laboratory (LLNL), as well as in 

Europe at the European Centre for Research and Advanced 

Training in Scientific Computation (CERFACS) in France 

and the Center for Computer Applications in AeroSpace Science and Engineering (C2

A2S2E) in Germany, with great 

success. Indeed, some of these centers include industrial 

funding in their model, further tying the institute to important 

stakeholders. One of the keys to the success of these institutes is that they are able to establish a facility and create a 

climate that fosters collaborations among government researchers and leading academics with the goal of advancing 

computational science and modeling of physics. The freedom 

that is afforded to the researchers while aligning broadly with 

the mission of the organization serves as a magnet for attracting the best talent from around the world, while ensuring 

relevance of the research. NASA should re-examine the role 

such institutes have played in the overall long-term success 

of computational methods within the agency and develop a 

new initiative to create an institute devoted to the advancement of both CFD and MDAO for NASA aeronautics, science, and space exploration mission directorate problems 

(see accompanying Case Study). The goal of the institute 

would be to broaden NASA interactions with the wider scientific community and to foster long-term collaborations 

with experts in important complementary fields. To be effective, the institute will require critical mass, sustained core 

funding over the long term, and the development of a reputation for excellence. One approach to building up this facility 

would be to start with seed funding for a sustained summer 

visitor program that would grow in size over several years, 

and which can be complemented with a small group of internal researchers or longer term visitors. 

Recommendation 6: NASA should attract world-class engineers and scientists. 

The ability to achieve the long-term goals for CFD in 2030 is 

greatly dependent on having a team of highly educated and 

effective engineers and scientists devoted to the advancement 

of computational sciences. This is particularly critical within 

NASA given the demographics of the current workforce. Opportunities to stabilize and 

expand CFD and simulation personnel in the 

future should be pursued 

to enable a renewed 

leadership role in CFD 

development including 

researchers and developers with diverse backgrounds (physical modeling, numerical algorithms, applied mathematics, 

computer science, software development, and various aerospace engineering application domains). Attracting this future generation of leaders will present challenges. To be successful, several suggestions are presented here. NASA currently has several fellowship programs in key areas throughout the agency, but none are specifically devoted to computational science. A NASA-focused fellowship program similar 

to the Department of Energy’s Computational Science Graduate Fellowship (DOE-CSGF)154 should be considered. In 

addition, having opportunities for longer term visits (e.g., 

summer or other) for students will also be important to continually attract the best aerospace talent: this is best achieved 

through formal visit programs with specific computationalscience goals, managed either directly through NASA or 

through supported research institutes. Finally, attempts to 

capture future generations of computational engineers and 

scientists can benefit from providing visiting students with 

the opportunity to meaningfully contribute to grandchallenge efforts that capture their imagination and are closely aligned with their values (environmental impact of commercial aviation, personal air vehicle, larger degrees of autonomy/UASs, and the sizable interest in high-speed vehicles 

including supersonics, hypersonics, and re-entry).
37 

8 Conclusions 

Despite considerable past success, today there is a general 

feeling that CFD development for single and multidisciplinary aerospace engineering problems has been stagnant for 

some time, caught between rapidly changing HPC hardware, 

the inability to predict adequately complex separated turbulent flows, and the difficulties incurred with increasingly 

complex software driven by complex geometry and increasing demands for multidisciplinary simulations. In this report, 

we have provided a knowledge-based vision of what future 

CFD capabilities could be, and indeed must be, in order to 

radically advance the aerospace design process and enable a 

new generation of more capable aerospace vehicles. This 

vision was used to identify important barriers and impediments, which in turn were used to formulate a long-term 

technology development plan. These findings were obtained 

with broad community input, including a formal survey, a 

community workshop, as well as through numerous informal 

interactions with subject matter experts. This information 

was distilled into a programmatic structure and a set of recommendations that are expected to be important for advancing the state-of-the-art CFD in particular and multidisciplinary simulations in general, while also achieving the Vision. 

Although some outcomes of this study point to specific technological solutions, many recommendations are simple and 

self-evident: robust support for basic simulation technologies, better access to leading-edge HPC hardware, better internal collaborations between aeronautics and space drivers, 

better coordination with other large computational science 

programs, and the need for innovative strategies to advance 

the research agenda in a resource-constrained environment. 

Many current large government agency programs in computational science can trace their roots to reports that originated 

from communities of experts, from the grassroots upwards, 

often based on input from community workshops, commissions, or private and public panels and testimonies. We have 

followed such a model in this work, with the realization that 

many such endeavors are not successful on their first attempt, 

but often require years of gestation. However, the broad 

community input, general consensus, and wide range of expert opinions coupled with a diverse experience base from 

academia, government, and industry that have contributed to 

this report make it a significant advocacy document. To ultimately be successful, periodic reviews of CFD technology 

development like this must be undertaken to continually 

drive the state of the art forward. 

9 Acknowledgments 

This study was performed under NASA contract number 

NNL08AA16B, task number NNL12AD05T with William 

Kleb as Contracting Officer Representative (COR) and Mujeeb Malik as Technical Monitor. The authors wish to thank 

the extended Vision 2030 CFD Study team: Joerg Gablonsky, Mori Mani, Robert Narducci, Philippe Spalart, and 

Venkat Venkatakrishnan, The Boeing Company, and Robert 

Bush, Pratt & Whitney, for their valuable technical contributions in the execution of the study and in the preparation of 

this document. Also, we would like to acknowledge the active participation of the attendees at the Vision 2030 CFD 

study workshop held in May 2013 at the National Institute of 

Aerospace (NIA), especially Paul Durbin, Iowa State University, Sharath Girimaji, Texas A&M University, and Brian 

Smith, Lockheed Martin Corporation, for their presentations 

on turbulence modeling. We are grateful for additional input 

provided by (in no particular order): Dave Schuster (NASA), 

Michael Aftosmis (NASA), Chris Rumsey (NASA), Joe 

Morrison (NASA), Jim Thomas (NASA), Manny Salas 

(NASA/ICASE retired), Jamshid Samareh (NASA), Reynaldo Gomez (NASA), Michael Hemsch (NASA), Earl Dowell (Duke University), Ron Joslin (US Navy), David Young 

(Boeing), Zhi Jian Wang (University of Kansas), Karthik 

Duraisamy (University of Michigan), Edwin van der Weide 

(University of Twente), Rob Falgout (LLNL), Laurent Cambier (ONERA), Sylvie Plot (ONERA), Bijan Mohammadi 

(CERFACS/Universite de Montpellier), Norbert Kroll 

(DLR), Cord Rossow (DLR), Kazuhiro Nakahashi (JAXA) 

and Atsushi Hashimoto (JAXA). Finally, we would like to 

thank all who participated in the Vision 2030 CFD survey for 

their valuable time and insightful comments. 

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APPENDIX A. High Performance Computing Trends and Forecast for 2030 

Introduction 

Computational Fluid Dynamics (CFD) codes utilize High 

Performance Computing (HPC) systems, so understanding 

where HPC technology might be in the 2030 timeframe is an 

important component of creating a vision for CFD codes in 

2030. Of course, forecasting where HPC technologies will be 

in the future requires a significant amount of extrapolation, 

which is especially hard in such a fast changing area as HPC. 

The fastest current systems can perform more than 10 petaFLOPS (1 petaFLOPS is 1015 floating point operations per 

second) and the HPC community is working toward systems 

capable of 1018 FLOPS (exaFLOPS), which are expected 

sometime between 2018 and 2023. Some work is even looking at 1021 FLOPS (zetaFLOPS). However, reaching that 

level of performance is unlikely without radically new technologies. 

A common, though controversial, measure of HPC systems is 

the total number of floating point operations a given system 

can perform in a second while solving a large linear system 

of equations using Gaussian elimination; this is the HP 

LINPACK benchmark. Twice a year a list of the top 500 

systems in the world against which those numbers are measured is published by the Top500 organization. The current 

list (June 2013) is topped by the Tianhe-2 system, developed 

by China’s National University of Defense Technologies, 

which achieved 33.86 petaFLOPS (quadrillions of calculations per second) on the LINPACK benchmark 

[Top500.org]. Here, we will estimate 

only the peak floating-point performance in terms of the maximum number of operations that can be performed 

per second. We note that the performance of many applications, including 

CFD applications, may be more accurately estimated by using sustained 

memory bandwidth;1

 for the purposes 

of this summary, we assume that other 

aspects of system performance, such as 

memory latency and bandwidth and 

integer operation performance, are provided in a similar ratio to today’s systems. This is a significant assumption 

and should be borne in mind when considering the predictions outlined in this 

summary. 

A significant measure of a processor is 

the feature size of its components. The 

smaller the features, the more elements 

can be placed in the same area, and 

hence the more powerful a processor 

becomes. Feature size also has a direct 

impact on power consumption, and heat generation, with 

smaller sizes being better. Thus, forecasting feature sizes of 

future processors is very important. Unfortunately, the industry has not always been good in that forecasting, which is one 

reason why predicting where HPC technology will be in 

2030 is particularly hard. For example, in 2005, the International Technology Roadmap for Semiconductors (ITRS) 

forecasted a 22-nm gate length by 2008; that is, the structures 

in a modern processor were forecast to have features with 

sizes around 22 nm. However, in 2008 the forecast date 

moved to 2011 and in 2011, it moved again to 2012. A similar slip occurred for other (smaller) gate lengths (see Figure 

4). Note that the forecasts of the ITRS combine inputs from 

all major chip manufacturers, equipment suppliers, and research communities and consortia, so it represents the combined wisdom of the industry. Nevertheless, as Figure 4 

shows, forecasting a key feature of even this basic component of processors is hard. The figure points out that Moore’s 

“Law” is really just an observation about engineering progress and offers no guarantee. There are serious concerns 

about the longevity of this law, especially when trying to 

extrapolate to 2030. 

To come to our final predictions of a HPC system in 2030 we 

go through a two-step process. We start with a prediction 

about a practical exascale system, likely in the 2020-2023 

time frame. To help with the forecasting, we incorporate 

some thoughts about the predictions made for a petascale 

system around 2000, and how they panned out. In the second 

step, we further extrapolate from this base to 2030. 

To help create a vision for a CFD Code in 2030, it is important to describe three different classes of HPC systems 

0

5

10

15

20

25

30

2007 2012 2017 2022 2027

Physical Gate Length, nm

Expected Manufacturing Year

2005

2008

2011

ITRS 

Forecast

Year

Figure 4. Changing Predictions About Semiconductor Sizes 
46 

that are of importance for the CFD community. First are the 

leadership class systems that reside at National Laboratories 

or other government agencies, such as NASA. These will be 

used to solve the hardest, most challenging problems that 

break new ground and drive basic understanding about flow 

phenomena and how to simulate them. The second class of 

systems is the type of systems large industrial companies like 

Boeing, Pratt & Whitney, or Airbus use. These are in general 

one to two orders of magnitude smaller than the leadership 

class systems. For example, Airbus entered a system at number 29 in the June 2011 Top500 list, with a capability about 

33 times smaller than the number one system on that list. 

Finally, the third class of systems consists of HPC systems 

that would be used by smaller companies, or individual departments of larger companies. These are again one to two 

orders of magnitude smaller than the systems in the second 

class. 

It is likely that similar technologies will be used by all of 

these classes of systems, with the performance scaling roughly with the size (number of nodes) of the system. The reason 

that the performance is not strictly proportional to system 

size is that the performance of the interconnect that ties all of 

the computing elements together does not scale with the size 

of the system, requiring either more advanced technologies at 

larger scale or providing lower overall performance at scale. 

Another critical component of HPC capability in 2030 is the 

advances in software infrastructure and programming methodologies that will be necessary to take advantage of these 

future HPC systems. The ultimate purpose for these systems 

is to solve the most pressing problems in academia and industry. In particular, industrial users pursue this technology 

because of the large impact on future product designs, and 

the ability to avoid or minimize the use of other, more costly 

methods such as wind tunnels or other types of physical tests. 

Petascale Predictions and What Happened 

Here we consider the predictions that were made in the 1990s 

about the first petascale systems: which of them proved true 

and which of them proved false. 

The following statements are from “Enabling Technologies 

for PetaFLOPS Computing” (1995): 

1. “The software for the current generation of 100 GF machines is not adequate to be scaled to a TF...” 

2. “The petaFLOPS computer is achievable at reasonable 

cost with technology available in about 20 years 

[2014].” 

3. “Software technology for [Massively Parallel Processors] MPP’s must evolve new ways to design software 

that is portable across a wide variety of computer architectures. Only then can the small but important MPP 

sector of the computer hardware market leverage the 

massive investment that is being applied to commercial 

software for the business and commodity computer market.” 

4. “To address the inadequate state of software productivity, there is a need to develop language systems able to 

integrate software components that use different paradigms and language dialects.” 

Of these predictions, only number 2, a statement about computer hardware, proved true, as systems with a peak performance of a petaFLOP were delivered in 2008 and achieved 

sustained performance in 2012.2

 It is notable that in 1995, it 

was predicted that the clock speed of a processor would be 

700MHz—well under what was achieved by commodity 

processors, but exactly the speed of the processors in the 

IBM BlueGene/L system—a clock speed chosen as the optimal one for performance at a given power. Also notable is 

that programming for a petascale system was expected to 

need new approaches, with nine overlapping programming 

models, including shared memory, message passing, data 

parallel, distributed shared memory, functional programming, 

object-oriented programming, and evolution of existing languages, considered essential. 

Observe that while the predictions about hardware were reasonable, those about software (1, 3, and 4) were not supported by quantitative data and turned out to be far too pessimistic. This is not to say that there is not a software productivity 

problem, but that it has not prevented the use of petascale 

systems, several of which are now in operation and are successfully performing computations in science and engineering. Given this experience, great care must be taken in making assumptions about what software might work (if not easily) and what is truly inadequate for exascale systems and 

beyond. 

Exascale Background 

An exascale system is one capable of 1018 operations per 

second, roughly 100 times as fast as the most powerful systems today. Several factors suggest that an exascale system 

will not just be a simple evolution of today’s petascale systems: 

1. Clock rates. Clock rates for commodity logic have plateaued, in large part because of leakage currents. This 

implies that increasing performance will be tied to increasing parallelism, as has been true since about 2006. 

It is unlikely that a new technology will be available by 

2023 to provide an alternative with faster clock rates. 

Rapid Single Flux Quantum (RSFQ), a technology using 

superconducting devices, could provide 250GHz gates, 

but bringing that technology to sufficient maturity, including density and cost, is unlikely within 10 years. 

With a sustained investment, it might be available by 

2030, but we still view this as unlikely to be a mature 

technology by 2030. 

2. Power consumption. Current petascale systems are consuming on the order of 10-20 megawatts (about 1 

MW/PF), so scaling current technology would require 1 

gigawatt for an exascale system (announced targets are 
47 

between 20 and 60 MW for an exascale system). Contributors to power consumption include: 

a. Processor Speed – slower processors are more power efficient (to a point); this implies even greater 

concurrency to reach a given level of performance. 

Processors may be in the 1 to 20 GHz range, with 

the most likely range being 1 to 5 GHz. 

b. Complex computing elements—features used to 

improve scalar performance, such as speculation, 

caches, and out-of-order execution—all have low 

power efficiency for the compute benefit they deliver. Processing elements are likely to be simpler and 

optimized for particular computing patterns. For example, there may be separate scalar, vector, and 

stream computing elements. GPUs already exploit 

the advantages of being specialized. 

c. Memory, based on the current DRAM architecture, 

consumes a surprising amount of power. As a result 

(and combined with the need for increased parallelism), there is likely to be both much less memory 

per processing element and much less memory total; for example, an exascale system may have only 

10 PB of memory. 

d. Moving data anywhere takes power, even within a 

“node” (e.g., between local memory and the nearest 

processing units). This will argue for much greater 

data locality in the choice of algorithms and their 

implementation. 

3. Fault tolerance and resiliency. This is a tricky subject 

and there is a great deal of misinformation about it. A 

common analysis is to take the failure rates of today’s 

systems (particularly commodity cluster systems) and 

extrapolate to a system built with the same parts but 100 

to 1,000 times as large, based on the number of processing elements expected in an exascale system. However, failure rates are more dependent on the number of 

parts (e.g., chips), not gates, and experience with some 

of the largest systems, such as the IBM Blue Gene systems, bears this out. Parts intended for the commodity 

market may accept higher rates of faults than what is acceptable for a large-scale, reliable exascale system. Having said that, there are reasons why an exascale system 

may have a higher rate of faults. For example, some 

techniques being proposed to reduce power consumption 

may raise the rate of failures. 

4. Performance regularity and scalability. Because of the 

extreme degree of parallelism required, scalability will 

be a major issue. Approaches that work with 1,000 or 

even 10,000 nodes may fail to perform well on an exascale system. In addition, several approaches under 

consideration suggest that the performance of the compute elements may be less predictable than it is now 

(e.g., using dynamic frequency adjustment to improve 

power efficiency). As a result, algorithms will not be 

able to decompose work based on any assumption about 

uniform performance or work. Adaptivity will be required in the algorithms and implementations. 

5. Latency tolerance. References to all memory, both local 

and remote, will take 100s to 10,000s of cycles. For remote references, much of this is speed-of-light delays, 

and can only be solved by making the entire machine 

physically smaller, which is unlikely in the next 10 

years. For more local references, this is a result of the 

memory hardware. Most novel memory techniques that 

may increase available memory size and/or reduce power consumption, also increase the latency for memory 

accesses. In fact, latencies of hundreds of cycles are 

common today in microprocessors, but much of this is 

hidden from the programmer through the use of memory 

caches and prefetch hardware. 

Sample Exascale Architecture 

An exascale computer might look something like this: 

Each node contains 16 1-GHz simple scalar processors, each 

with an integrated, 1,000 core streaming processor (also 1 

GHz). At the memory interface is another 1,000 core streaming processors (but with more limited operations, also at 1 

GHz). This gives 128 TFLOPS per node (assuming fused 

multiply-adds, 2 per cycle). 10,000 of these nodes bring you 

to 1 exaFLOPS. The interconnect may be a combination of 

electrical and optical (chosen to provide power-efficient 

bandwidth) using high-radix routers, similar to what is used 

in the Blue Waters Supercomputer at NCSA. It may also be a 

3D torus (between the nodes), but allowing each link to be 

used concurrently, as in the IBM Blue Gene/P systems. 

Note the reliance on “stream” processing; you can think of 

this as a distributed memory vector processor, where virtually all of the work must be suitable for the vector/stream processing elements (those 1,000-core components). Today’s 

graphics processing units, as well as Intel’s Xeon Phi (MIC) 

chips, can be considered examples of stream processors. 

Bisection bandwidth relative to peak performance is likely to 

be much smaller than in today’s systems. However, there 

may be support for some critical global operations, such as a 

nonblocking allreduce or nonblocking barriers. These global 

operations might be underappreciated, but might be particularly useful for special cases, for example for distributed termination detection. 

Other systems will have a different balance, for example, 

more scalar (or short vector) compute units, more nodes but 

with less parallelism per node. Operation mixes may be different, e.g., more support for integer operations at the expense of floating point, or specialized integer units. (Such a 

different approach is shown in Table 1 in the prediction for 

an exascale system in 2023). However, it is very unlikely that 

an exascale system would look much like an IBM Blue Gene, 

Cray XE/XK, or IBM Productive, Easy-to-use, Reliable 

Computing System (PERCS), which is officially known as 

Power 775.3

 From a functional standpoint, an exascale sys-
48 

tem is likely to have heterogeneous functional elements, each 

optimized to different styles of computing. The closest current systems are GPU clusters, such as RoadRunner at Los 

Alamos National Laboratory with IBM PowerXCell accelerators, Titan at Oak Ridge National Laboratory with NVIDIA GPUs, or Stampede at the Texas Advanced Computing 

Center with Intel Xeon Phi (MIC) coprocessors. However, an 

exascale system will be much more tightly integrated; it will 

not have accelerators and coprocessors as loosely connected 

to the rest of the system, as is the case in current offerings. 

An all-accelerator/coprocessor-like system is possible but 

unlikely (consider the above sample system, but with no scalar processors). Exascale systems may well have CPU-like 

and accelerator/coprocessor-like elements on the same chip 

as described in the first paragraph. 

Programming in Exascale 

Programming languages take many years to develop. It is 

very unlikely that a new programming model will be developed in time for the first exascale systems. What is possible 

and even likely is that higher-level, special-purpose languages will be developed to help write efficient code for 

these systems. Applications will be a mix of current programming models (C/C++/Fortran), combined with Message 

Passing Interface (MPI) and OpenMP, possibly Unified Parallel C (UPC) and Co-Array Fortran (CAF), now partially 

integrated into Fortran 2008, combined with specialty languages for particular computation styles, like Compute Unified Device Architecture (CUDA) or OpenCL, algorithm and 

data-structure specific code writing systems like the Tensor 

Contraction Engine (TCE),4

 and runtimes implementing other programming techniques (e.g., Intel’s Thread Building 

Blocls (TBB) for intranode parallelism and CHARM++ for 

general parallelism). Further developments to improve the 

programming of accelerators and coprocessors through directive-based concepts as defined in OpenACC and future 

versions of OpenMP will play an important role, especially 

since they are addressing some of the portability concerns of 

software developers. Finding the right balance between general programming language support and more limited but less 

complex tools sufficient to achieve performance will be an 

important part of any exascale application development. Such 

special features may include higher level programming models for the “stream” or vector computing elements or support 

for software and/or algorithm assisted fault tolerance. 

There have been efforts to develop new approaches for programming high-performance computing systems. The 

DARPA High Productivity Computing System (HPCS) project had a goal of a tenfold increase in productivity through a 

combination of new programming languages and new hardware capabilities. While interesting research came out of the 

language efforts (particularly Cray’s Chapel and IBM’s X10 

languages), these have yet to provide users with viable alternatives to existing models. Outside of a few specialized areas, the adaptation of partitioned global address space (PGAS) 

languages such as UPC is very low. The reality is that creating a truly new language is a long-term project, and is unlikely to be completed before the first exascale systems appear. 

More likely is the evolution and enhancement of existing 

languages, including extensions to MPI (e.g., MPI-3 now 

provides access to shared memory regions) and to existing 

programming languages (e.g., OpenACC is a small extension 

to C/C++ and Fortran). There is an opportunity to develop 

new programming systems for 2030, but only if work starts 

soon on the necessary research. 

Other Issues 

File input/output (I/O) is another issue. Many of the same 

issues apply (power, latency, smaller ratio of space/FLOP). 

Current approaches based on blocking I/O to a single file per 

process will not be effective. At the scale of these future systems, it will probably be necessary to have a subset of processors perform I/O for groups of processors, preferably in 

parallel to the computation. This is another example of specialization, this time at the software level. 

Finally, while an exascale system can act as 1,000 petascale 

systems (or a million terascale systems), this is unlikely to be 

an efficient use of the system. Simple approaches to ensemble calculations that can be executed serially on a collection 

of much smaller systems do not constitute an exascale calculation (regardless of their scientific importance). 

HPC in 2030 

To extrapolate computer performance to 2030, we have made 

the following assumptions. These are for a conservative design, and provide a likely minimum performance level for 

2030: 

1. The 2012 International Technology Roadmap for Semiconductors (ITRS), which has predictions out to 2026, 

can be extended to 2030. 

2. Computer organization will be similar to current systems 

that integrate multiple processor types, but with greater 

degrees of integration. Specifically, we postulate that a 

system will contain nodes that integrate a fast scalar processor, a stream processor, and processing in memory 

(PIM). 

3. Processing elements have a constant number of devices 

and the size of a chip is roughly constant. Thus, the 

number of processing elements per chip increases with 

the square of the ratio of gate feature size. 

4. The many engineering challenges required to achieve the 

ITRS targets will be met. 

Table 1 shows estimated performance in 2012, 2020, 2023, 

and 2030. This estimate is consistent with current leading 

systems; both IBM Blue Gene/Q and Cray XK7 systems 

achieve around 20 PetaFLOPS peak. The estimate for 2023 is 

consistent with some current DOE estimates, providing a 

little more than 1 exaFLOPS. By assuming a significant increase in processor density, we estimate that performance 
49 

between 16 to 32 exaFLOPS may be achievable by 2030. 

Note that there are many assumptions in this estimate, and 

many yet unsolved engineering problems must be overcome 

to maintain the targets in the ITRS roadmap. In addition, we 

have assumed lower clock rates in the stream and processorin-memory elements, reflecting a different optimization point 

for speed and energy use. 

It is important to note that these predictions are sensitive to a 

number of hard-to-forecast values. For example, energy and 

power dissipation problems could reduce the number of processing units that can be assembled into a single system, reducing total performance.5

 Conversely, new 3D fabrication 

and packaging could increase the density of components, 

allowing even greater parallelism. The major conclusion that 

should be drawn from this table is that current trends will 

yield significantly faster systems than we have today, but not 

ones that are as fast as the past 20 years of development 

would suggest. 

Another important feature of an HPC system in this time 

frame we expect to see are even more levels of memory than 

we currently have. Current systems have up to three levels of 

cache, and then main memory. Systems with accelerators 

have additional memory attached to the accelerator. In 2030, 

main memory itself might be composed of different levels, 

with portions being very fast, but small, and other portions 

larger and slower. Combined with the concept of processing 

in memory, that is, having some computing capability embedded within the memory subsystem, this will lead to an 

even more complex overall system. 

Programming a 2030 HPC system 

Software has a much longer lifespan than hardware, and as 

pointed out earlier, the expectation is that there will be only 

evolutionary changes to the programming model in the 2020-

2023 timeframe. For 2030, the likelihood that some major, 

revolutionary changes to the programming models will occur 

is higher because of the extra development time. It is important to point out that this is not a guarantee, as many programming languages and models have shown a surprising 

level of sustainability. In addition, as we pointed out in the 

discussion on the validity of petascale projections, software 

advances are much tougher to predict than hardware advances. 

Future programming models will be driven by dealing with 

locality, whether they are new or extensions of existing programming models. Programmers need to be able to express 

locality and relationships between data abstractly. NVIDIA’s 

CUDA programming language is an example of a newer 

programming model that forces programmers to deal directly 

and explicitly with locality. This illustrates the need for the 

expression of locality while also showcasing the need for 

ways to express this information about locality more abstractly and portable. 

As discussed above, we pointed out that the memory system 

will probably become much more complex, both with the 

introduction of processing in memory (PIM) as well as with 

more levels of memory architectures. While some of this 

complexity will be hidden from the developers, a lot of it will 

not. The developers need to be able to express what computing should be done by the slower processing elements inside 

the memory subsystem, and what needs to be done by the 

fast scalar processor or the streaming elements. The processing elements within the memory subsystem will have 

significantly higher bandwidth to memory. One of the easiest 

uses to imagine of this processing is to perform calculations 

for prefetching of data (gather), and scatter the results of calculations back into the final locations in the memory subsystem. Because of the processing power and bandwidth envisioned in the memory subsystems, these can be significantly 

more complex than possible within the processors, which 

will be especially useful for software with complex memory 

access patterns, for example, unstructured CFD codes. 

We do not believe that there will ever be a programming 

model that completely hides the complexity of the underlying 

HPC system from the programmer while achieving the necessary performance. Nevertheless, we do think that great 

advances can be made to allow the programmer better to 

express her or his intent and to provide guidance to the compiler, runtime system, operating system, and even the underlying hardware. This will require significant research and that 

Table 1. Estimated Performance for Leadership-class Systems 

Year 

Feature 

size 

Derived 

parallelism 

Stream 

parallelism 

PIM parallelism 

Clock 

rate 

GHz FMAs

GFLOPS 

(Scalar)

GFLOPS 

(Stream)

GFLOPS 

(PIM) 

Processor 

per node 

Node 

(TFLOP) 

Nodes 

per 

system

Total 

(PFLOPS)

2012 22 16 512 0 2 2 128 1,024 0 2 1 10,000 23 

2020 12 54 1,721 0 2.8 4 1,210 4,819 0 2 6 20,000 241 

2023 8 122 3,873 512 3.1 4 3,026 12,006 1,587 4 17 20,000 1,330 

2030 4 486 15,489 1,024 4 8 31,104 61,956 8,192 16 101 20,000 32,401 

Feature size is the size of a logic gate in a semiconductor, in nanometers. Derived parallelism is the amount of concurrency, given processor cores with a 

constant number of components, on a semiconductor chip of fixed size. Stream and PIM parallelism are the number of specialized processor cores for 

stream and processor-in-memory processing, respectively. FMA is the number of floating-point multiply-add units available to each processor core. From 

these values, the performance in GigaFLOPS is computed for each processor and node, as well as the total peak performance of a leadership-scale system.
50 

research needs to start now for solutions to be ready in the 

2030 time frame. 

Related to locality is the fact that the developer community 

needs to change their thinking away from a focus on floating 

point operations. In the 2030 time frame, FLOPS might be 

considered “free,” and data movement, synchronization, and 

all levels of parallelization will become the driving forces for 

performance. We already see this to some extent with current 

accelerators like the GPUs from AMD and NVIDIA. We 

need to start looking at the quality of algorithms from the 

point of view of arithmetic intensity, that is work per 

memory access, rather than just looking at floating point operations. Prime examples of algorithms that have, in general, 

relatively low arithmetic intensity are sparse linear algebra 

methods. Utilizing the processors in the memory subsystem 

could increase the arithmetic intensity by delivering the right 

data to the scalar and streaming processors in a contiguous 

manner. Of course, as we see today, there will be codes covering the full range from highly optimized codes that run on a 

single architecture to codes that are highly portable, but not 

as high performing. 

One concept to determine a “sweet-spot” at exascale is to 

develop more composable programming models. The lowlevel components will be highly optimized for a given architecture, probably even by the vendor itself, and the higher 

level applications that build on these low-level components 

are significantly more portable. Examples of this are Intel’s 

MKL, or PETSc (Portable, Extensible Toolkit for Scientific 

Computation6

) from Argonne National Lab. While achieving 

high levels of performance will never be a 100% automated 

process, such a composable programming model should allow the development of transportable software, that is software that can be ported easily from one platform to the next, 

while still requiring optimizations to achieve full performance. 

Another concept that will become important for software will 

be specialization within applications. As pointed out earlier, 

it might be necessary to have dedicated processes dealing 

with I/O in parallel to the computation. Other processes 

might analyze or process the data generated by the main algorithm on the fly, and only the processed data is actually 

stored. For example, visualizations of results and calculations 

of derived properties might be done in parallel with the main 

calculations rather than after the main simulation finishes. On 

a lower level, separate processes might be used to gather data 

for upcoming calculations, and scatter the results of calculations as mentioned above. This will be especially important 

considering the extreme levels of parallelism we forecast the 

hardware will provide in 2030. 

With the increased complexity comes the need for improved 

programming tools like profilers, compilers, and debuggers. 

These need to be (relatively) easy to use and allow the developer a deep understanding of the behavior of their codes and 

the barriers to good performance on a given system. Having 

the ability to inform the developer of the inhibitors in order to 

move software to the next generation of HPC systems and of 

the changes to make that will allow good performance on 

both current and future systems will significantly increase the 

productivity of the developers and utilization of future HPC 

systems. 

This leads to the need for a well-trained developer workforce. 

Even application developers utilizing libraries or advanced 

programming models need to understand the basic principles 

of parallelism and the need to utilize and express locality and 

the other demands on software by the hardware in 2030. We 

also need developers that can build and optimize the lower 

level components of the software architectures. These developers must have a deep understanding of the hardware architectures, as well as work closely with the application developers to provide the high-level components they need. 

Alternative Computer Architectures 

Up to this point, our analysis is based on the evolution of 

current technology. Such evolution has provided an exponential increase in performance over several decades; while there 

are many challenges in continuing the same rate of increase, 

the assumptions in this report represent a likely path for 

computer architecture. However, other device technologies 

could give rise to computers with very different capabilities. 

A few that were discussed include: 

1. Quantum Computers. There is steady progress on fabricating practical quantum computers, and such systems 

may be available in 2030. However, while a quantum 

computer can be used for some linear algebra calculations (after all, the Schrodinger equation involves linear 

operators), a quantum computer is not necessarily a faster computer for CFD calculations. 

2. Superconducting logic. For example, Rapid Single Flux 

Quantum (RSFQ) logic gates were demonstrated at over 

770 GHz, and 100 GHz gates are available now. A 

drawback of this device technology (as currently implemented) is significantly lower density; as an immature 

technology, cost is also an issue. 

3. Low-power memory. Many novel memory designs are 

being developed that use something other than charge to 

store data. Some have much higher latencies but provide 

much lower power use and higher densities of storage. 

4. Massively parallel molecular computing. This is a 

very different paradigm, and uses far higher levels of 

parallelism (typically 1023) but also gives up determinism. It is not clear how to cast CFD calculations into a 

form suitable for molecular computing. 

Many of these revolutionary architectures will also require 

revolutionary changes to the full software ecosystem, especially quantum computers and molecular computing. Considering the long development timeframes for software, early 

examples of these technologies need to be available to a larger developer community in the 2020-2023 time frame to en-
51 

sure that these new architectures will have broad impact on 

more than a very small subset of the HPC user community. 

Moreover, while we can foresee significant progress in pushing HPC technology to the next level using approaches that 

are more evolutionary until the 2030 timeframe, we are much 

more skeptical for the time after 2030. As we pointed out 

earlier in the evolutionary approach, the semiconductor industry predicts feature sizes of 4 nm. This means that a feature will consist of small numbers of atoms, and significant 

quantum effects will play a role. An end of the ability to further shrink feature size is clearly in sight at that time. Even if 

the above listed revolutionary changes are not necessary to 

reach goals for 2030, they are certainly important for allowing us to move beyond 2030. Some technologies might not 

seem attractive now (e.g., too expensive, too slow, too hard 

to program) but we need to invest in them to overcome those 

faults to be able to take advantage of their benefits. 

Research Suggestions 

We conclude with a list of research that needs to be started 

now and in the coming years to enable our predictions of 

HPC in 2030 to be realized. While not complete, this list is a 

good starting point for the community. There is no order of 

importance implied in this list. We need to develop and implement all the items in this list and then demonstrate them 

on important use cases. 

 Alternate Hardware Technologies 

 Quantum Computers 

 Superconducting logic 

 Low-power memory 

 Massively parallel molecular computing 

 Next generations of “traditional” processor technologies 

 On-chip optics 

 Advanced memory technologies (e.g., 3D memory) 

 Advanced Algorithms 

 Data movement aware (not FLOPS oriented) algorithms 

 Power aware algorithms 

 Advanced Programming Models and Systems 

 Locality aware, abstract programming models 

 Composable programming models 

 Transportable, extremely parallel programming models 

 Transportable, extremely parallel HPC software 

 Highly scalable and manageable data management 

systems 

 Compiler interfaces that allow better expressions of 

developer intent 

 Improved programming tools like compilers, profilers and debuggers 

________________________

1

 Anderson, W. K., Gropp, W. D., Kaushik, D. K., Keyes, 

D. E., and Smith, B. F., “Achieving High Sustained 

Performance in an Unstructured Mesh CFD Application”, 

Proceedings of the ACM/IEEE SC99 Conference on High 

Performance Networking and Computing,1999, IEEE 

Computer Society. 

2

 The exact dates for these achievements depend on your 

definition of peak and sustained performance. 

3

 Wikipedia article on PERCS: 

http://en.wikipedia.org/wiki/PERCS

4

 See: S. Hirata, J. Phys. Chem. 2003, 107 (46), 9887-9897. 5

 Esmaeilzadeh, H., et al., “Power challenges may end the 

multicore era”, Commun. ACM, 2013. 56(2): p. 93-102. 6

 PETSc (Portable, Extensible Toolkit for Scientific 

Computation) homepage, http://www.mcs.anl.gov/petsc/
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CFD Vision 2030 Study: A Path to Revolutionary Computational 

Aerosciences 

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 NNL08AA16B 

 6. AUTHOR(S)

Slotnick, Jeffrey; Khodadoust, Abdollah; Alonso, Juan; Darmofal, David; 

Gropp, William; Lurie, Elizabeth; Mavriplis, Dimitri

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NASA Langley Research Center 

Hampton, Virginia 23681 

 

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National Aeronautics and Space Administration

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14. ABSTRACT

This report documents the results of a study to address the long range, strategic planning required by NASA's Revolutionary Computational Aerosciences 

(RCA) program in the area of computational fluid dynamics (CFD), including future software and hardware requirements for High Performance Computing 

(HPC). Specifically, the "Vision 2030" CFD study is to provide a knowledge-based forecast of the future computational capabilities required for turbulent, 

transitional, and reacting flow simulations across a broad Mach number regime, and to lay the foundation for the development of a future framework and/or 

environment where physics-based, accurate predictions of complex turbulent flows, including flow separation, can be accomplished routinely and efficiently in 

cooperation with other physics-based simulations to enable multi-physics analysis and design. Specific technical requirements from the aerospace industrial 

and scientific communities were obtained to determine critical capability gaps, anticipated technical challenges, and impediments to achieving the target CFD 

capability in 2030. A preliminary development plan and roadmap were created to help focus investments in technology development to help achieve the CFD 

vision in 2030.

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Aerodynamics; Aerothermodynamics; Computational Fluid Dynamics; High Performance Computing; Propulsion; Space 

Exploration

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