8 Budgetary

Section 8: Budgetary Considerations

A clear challenge to this P5 was to realize our vision within the provided budget scenarios. We carried this out with clear principles of prioritization. Below are the rationales for the choices we made for the baseline scenario and for the less favorable scenario.

8.1Prioritization Principles

In the process of prioritization, we considered scientific opportunities, budgetary realism, and a balanced portfolio as major decision drivers.

Clear principles for the prioritization of scientific opportunities guided the deliberations of P5, as outlined in section 1.6. In addition, depending on project scale, our minimum requirements were:

Large projects (>$250M)

Medium projects ($50M–250M)

Small projects (<$50M)

To provide us with a fair and dependable basis for evaluating big projects, we set up a subcommittee with project experts from the physics community, which reviewed the maturity of cost estimates, the risk analysis and mitigation plans, and the proposed schedule. The subcommittee provided an expected cost range for each project and comments on project risks, budget maturity, and schedule. We also considered the uncertainties in the costs, risks, and schedule as part of our prioritization exercise. The prioritized project portfolios were chosen to fit within a few percent of the budget scenarios and to ensure a reasonable outlook for continuation into the second decade, even though that is beyond the purview of this panel.

Finally, we paid careful attention to the balance in the program in terms of:

Size and timescale of projects. Large projects push the boundaries of our capabilities and bring together broad communities of people. Small projects operate on shorter time scales, which provide crucial training and leadership opportunities for young scientists and have the potential for transformative breakthroughs.

Onshore vs offshore. Onshore projects can leverage the unique capabilities of US facilities and ensure our leadership. The global nature of our field necessarily means that we would like to participate in offshore projects for important physics experiments, with the benefits of lower cost and cooperation with international partners. Yet there are logistical and financial issues associated with the need to travel abroad frequently.

Project vs research. Projects are meant to produce cutting-edge data, which need to be analyzed and interpreted by activities in research. However, research is where new ideas and concepts are conceived of in order to guide the design of projects. In addition, research supports people, namely graduate students, postdocs, and scientists, and therefore requires an adequate level of funding to ensure the future health of the field.

Current vs future investment. The field relies on current projects to produce science, train people, and advance the field. Without careful investment in the future, our capabilities will diminish and the US will lose its global leadership. Future investments include technology, such as accelerators, detectors, and computing, as well as the theory that guides the field. The portfolio, like all investments, requires regular rebalancing.

8.2Hard Choices for Baseline Budget Scenario

The overall cost of the projects proposed during the Snowmass community study exceeded the budget scenario by many times. As a result, we had to make tough choices based on the principles stated above. We carefully selected projects that have the biggest scientific impact while maintaining the balance among science areas and satisfying the budgetary constraints, resulting in an exciting program for the next ten years. The baseline budget scenario assumes an initial bump in the budget thanks to the CHIPS and Science Act, and an annual 3% increase to keep pace with inflation.

The following project list reflects the sacrifices made in P5’s prioritization process, starting with the largest and moving down to the funding level of approximately $100M.

Onshore Higgs factory. We could not identify room in the budget executable in the next 20 years for an onshore Higgs factory unless the overall budget is several times higher. On the other hand, there is an ongoing process in Europe to see if FCC-ee is feasible. The Japanese HEP community has been making an effort to realize ILC as a global project hosted in Japan. We therefore recommend exploring offshore options and vigorously pursuing international collaborations so the US can play a major role when one of those projects becomes reality. If FCC-ee and ILC are judged to be not feasible, a new panel should revisit the possibility of bidding to host a Higgs factory in the US, potentially as a global project and including advanced technology options.

Fermilab Accelerator Complex Extension Booster Replacement (ACE-BR). Extending the capability of the accelerator complex is important to secure the future of particle physics. Unfortunately, the cost of the proposed options was prohibitive for the given time period. Additionally, it is not yet clear how the extension will enhance Fermilab’s capability to support future high-energy colliders, which are key to this report’s long-term vision. We therefore recommend MIRT, a less expensive option that achieves 2.1 MW of beam power (instead of 2.4 MW) earlier than envisioned by ACE-BR, augmented by a reliability upgrade (section 6.6.2) of the current booster to provide the required beam for DUNE.

DUNE FD4. As described in sections 3.1.3 and 3.1.4, the re-envisioned plan for DUNE Phase 2 enables DUNE’s science goals to be achieved with only three LAr far detector modules in the 2040s time frame. It also provides an opportunity for the FD4 to host a different type of detector or enhanced LAr detector to expand the science program of DUNE, leveraging the deep underground site and powerful beam. This budget scenario can accommodate only R&D for FD4 during this period.

One of two G3 experiments for direct detection of WIMP dark matter. TThere were two major proposals for dark matter experiments with sensitivity to reach the neutrino fog, envisioned to be the ultimate sensitivity achievable with the current technology. Even though the two proposals are attractive, we cannot accommodate both in this budget scenario. We recommend that the US bids to host one G3 experiment at a new cavity at SURF. If the bid fails, the US should become a leading partner in one outside the US. If the funding situation is better than in the baseline scenario, or if NSF or other partners can make a substantial contribution, or if an experiment shows a hint of a detection, a second experiment may be considered, possibly outside the US.

Spec-S5. This project follows the current world-leading project DESI and the follow-up DESI-II program to significantly enhance the sensitivity to the physics behind dark energy, dark matter, and inflation. We endorse the scientific objectives of the proposal, but it, including the cost estimate, was not sufficiently mature to recommend it. Instead, we recommend support for R&D on smaller fiber positioners to take spectra of a much larger number of objects simultaneously and to define the survey concept and required telescopes. In a more favorable budget scenario, the project may be considered once its scope is well-defined and technical feasibility has been demonstrated.

Mu2e-II. Mu2e extends the discovery reach for charged lepton flavor violation by four orders of magnitude, while Mu2e-II is proposed to further extend it by another order of magnitude. Mu2e, once in operation, will take data until 2034. Considering budget reality, scientific case, and the need for informed design choices, we recommend R&D and await the outcome and performance of Mu2e before starting to fund Mu2e-II.

srEDM. Electric dipole moment experiments are powerful searches for quantum imprints at higher energy scales. A rich program of EDM searches exists within other DOE programs. We judge that the science case for HEP to enter this area needs to mature, especially relative to the cost of such a program.

MATHUSLA. By exploiting the HL-LHC beam by placing a detector away from the collision point, MATHUSLA has a large discovery potential. It does require commitment from CERN for civil engineering, which is yet to be decided. If downsized, it would qualify as a candidate in the ASTAE portfolio.

Forward Physics Facility. This item has a broad physics program utilizing the beam of HL-LHC by placing detectors at the forward direction from the collision point. The facility does require commitment from CERN for civil engineering, which is yet to be decided. The bundled request for the US funding of the FPF trio of experiments does not fit into our budget. However, individual experiments in the facility can be candidates in the ASTAE portfolio.

Some of the tough choices about which projects to include were based on the need to rebalance the portfolio to allow for research in underfunded areas of theory, instrumentation, computing, GARD, a new program for agile experiments, and a virtually non-existent targeted collider R&D program.

8.3Difficult Choices for Less Favorable Budget Scenario

The less favorable budget scenario assumes a 2% increase in budget per year, which does not keep pace with the assumed 3% annual inflation. Actual inflation may be even higher. In this scenario, we had to make harder choices than those made for the baseline budget scenario. We can maintain a minimum portfolio to continue some scientific progress, although US leadership will begin to erode in much of the field, jeopardizing our 20-year vision for the US particle physics program. Impacts on some of the major projects are described below:

Reduced contribution to an offshore Higgs factory. The US contribution will be reduced and the US cannot play a commensurate role as an international partner in the project.

DUNE FD3 with deferred ACE-MIRT. This scenario explicitly forces a delay in the DUNE Phase 2 timeline of execution, making the project less competitive and hurting the US reputation as a host for large international projects. In a technically limited schedule, the order of phase II elements is MIRT, FD3, and MCND. There is a compelling science case for these three components and hence when budgets allow this would be the preferred order of construction. If, on the other hand, budgets are more constrained, trade-offs also have to consider the science lost. In the long run the same statistics for the beam physics would be obtained by the addition of either MIRT or FD3. However, FD3 offers a broader set of science topics related to non-beam physics like supernovae and also has a better potential of attracting international support than MIRT. Therefore, in a budget-constrained scenario FD3 is prioritized over MIRT. MCND requires the combined statistics of FD3 and MIRT to accomplish its main goals and hence in all scenarios is the third priority. This scenario is also based on the understanding that MIRT and MCND can be added at any time to the program should additional funds become available. In all scenarios we preserve long-lead-time MIRT elements to enable staging of the beam.

G3 experiment outside the US for direct detection of WIMP dark matter. One G3 experiment for direct detection of WIMP dark matter can be supported at less than 50% level and only outside the US so that the SURF expansion is not needed. The US will cede its leadership in this area..

Reduced increase in support for research. We identified four areas in which the current support for research requires reinforcement to regain or sustain US leadership: theory, general accelerator R&D, instrumentation, and computing. This scenario would reduce the level of this critically needed reinforcement.

8.4US Support for Scientific Discovery

The field of particle physics entails curiosity-driven research that relies heavily on federal funding, which comes from taxpayers. We are grateful for that support.

This report discusses the difficult choices we made in our recommendations to maximize science output and make necessary investments in the future of the field with a long-term vision. Note that even a modest increase in the particle physics budget will allow for additional pathways to discovery by expanding the scope of science areas, accelerating projects, and investing more vigorously in the future. We listed additional opportunities in section 2.6.2.

Research in particle physics has an excellent track record of producing revolutionary technologies that enrich society as a whole (section 6.8). Pushing the boundaries of human knowledge requires bringing technology to the next level and training the next generation of scientists to become a technologically advanced workforce. Cutting-edge quantum technologies and AI advances are commonplace in particle physics. People trained in the field become a technologically advanced workforce in many areas of society. Knowledge is its crucial element. Investment in all areas of curiosity-driven research is critical for this foundation.

We are keen to bring knowledge and excitement of major innovations and discoveries to the people who paid for them. Join us as we explore the quantum universe.