Quantum Algorithms: A Call To Action

Quantum computing finds itself in a peculiar situation. On the technological side, after billions of dollars and decades of research, working quantum computers are nearing fruition. But still, the number one question asked about quantum computers is the same as it was two decades ago: What are they good for? The honest answer reveals an elephant in the room: We don’t fully know yet. For theorists like me, this is an opportunity, a call to action.

Technological momentum

Suppose we do not have quantum computers in a few decades time. What will be the reason? It’s unlikely that we’ll encounter some insurmountable engineering obstacle. The theoretical basis of quantum error-correction is solid, and several platforms are approaching or below the error-correction threshold (Harvard, Yale, Google). Experimentalists believe today’s technology can scale to 100 logical qubits and gates—the megaquop era. If mankind spends $100 billion over the next few decades, it’s likely we could build a quantum computer.

A more concerning reason that quantum computing might fail is that there is not enough incentive to justify such a large investment in R&D and infrastructure. Let’s make a comparison to nuclear fusion. Like quantum hardware, they have challenging science and engineering problems to solve. However, if a nuclear fusion lab were to succeed in their mission of building a nuclear fusion reactor, the application would be self-evident. This is not the case for quantum computing—it is a sledgehammer looking for nails to hit.

Nevertheless, industry investment in quantum computing is currently accelerating. To maintain the momentum, it is critical to match investment growth and hardware progress with algorithmic capabilities. The time to discover quantum algorithms is now.

Empowered theorists

Theory research is forward-looking and predictive. Theorists such as Geoffrey Hinton laid the foundations of the current AI revolution. But decades later, with an abundance of computing hardware, AI has become much more of an empirical field. I look forward to the day that quantum hardware reaches a state of abundance, but that day is not yet here.

Today, quantum computing is an area where theorists have extraordinary leverage. A few pages of mathematics by Peter Shor inspired thousands of researchers, engineers and investors to join the field. Perhaps another few pages by someone reading this blog will establish a future of world-altering impact for the industry. There are not many places where mathematics has such potential for influence. An entire community of experimentalists, engineers, and businesses are looking to the theorists for ideas.

The Challenge

Traditionally, it is thought that the ideal quantum algorithm would exhibit three features. First, it should be provably correct, giving a guarantee that executing the quantum circuit reliably will achieve the intended outcome. Second, the underlying problem should be classically hard—the output of the quantum algorithm should be computationally hard to replicate with a classical algorithm. Third, it should be useful, with the potential to solve a problem of interest in the real world. Shor’s algorithm comes close to meeting all of these criteria. However, demanding all three in an absolute fashion may be unnecessary and perhaps even counterproductive to progress.

Provable correctness is important, since today we cannot yet empirically test quantum algorithms on hardware at scale. But what degree of evidence should we require for classical hardness? Rigorous proof of classical hardness is currently unattainable without resolving major open problems like P vs NP, but there are softer forms of proof, such as reductions to well-studied classical hardness assumptions.

I argue that we should replace the ideal of provable hardness with a more pragmatic approach: The quantum algorithm should outperform the best known classical algorithm that produces the same output by a super-quadratic speedup.¹ Emphasizing provable classical hardness might inadvertently impede the discovery of new quantum algorithms, since a truly novel quantum algorithm could potentially introduce a new classical hardness assumption that differs fundamentally from established ones. The back-and-forth process of proposing and breaking new assumptions is a productive direction that helps us triangulate where quantum advantage lies.

It may also be unproductive to aim directly at solving existing real-world problems with quantum algorithms. Fundamental computational tasks with quantum advantage are special and we have very few examples, yet they necessarily provide the basis for any eventual quantum application. We should search for more of these fundamental tasks and match them to applications later.

That said, it is important to distinguish between quantum algorithms that could one day provide the basis for a practically relevant computation, and those that will not. In the real world, computations are not useful unless they are verifiable or at least repeatable. For instance, consider a quantum simulation algorithm that computes a physical observable. If two different quantum computers run the simulation and get the same answer, one can be confident that this answer is correct and that it makes a robust prediction about the world. Some problems such as factoring are naturally easy to verify classically, but we can set the bar even lower: The output of a useful quantum algorithm should at least be repeatable by another quantum computer.

There is a subtle fourth requirement of paramount importance that is often overlooked, captured by the following litmus test: If given a quantum computer tomorrow, could you implement your quantum algorithm? In order to do so, you need not only a quantum algorithm but also a distribution over its inputs on which to run it. Classical hardness must then be judged in the average case over this distribution of inputs, rather than in the worst case.

I’ll end this section with a specific caution regarding quantum algorithms whose output is the expectation value of an observable. A common reason these proposals fail to be classically hard is that the expectation value exponentially concentrates over the distribution of inputs. When this happens, a trivial classical algorithm can replicate the quantum result by simply outputting the concentrated (typical) value for every input. To avoid this, we must seek ensembles of quantum circuits whose expectation values exhibit meaningful variation and sensitivity to different inputs.

We can crystallize these priorities into the following challenge:

The Challenge
Find a quantum algorithm and a distribution over its inputs with the following features:
— (Provable correctness.) The quantum algorithm is provably correct.
— (Classical hardness.) The quantum algorithm outperforms the best known classical algorithm that performs the same task by a super-quadratic speedup, in the average-case over the distribution of inputs.
— (Potential utility.) The output is verifiable, or at least repeatable.

Examples and non-examples

Hamiltonian simulation is perhaps the most widely heralded source of quantum utility. Physics and chemistry contain many quantities that Nature computes effortlessly, yet remain beyond the reach of even our best classical simulations. Quantum computation is capable of simulating Nature directly, giving us strong reason to believe that quantum algorithms can compute classically-hard quantities.

There are already many examples where a quantum computer could help us answer an unsolved scientific question, like determining the phase diagram of the Hubbard model or the ground energy of FeMoCo. These undoubtedly have scientific value. However, they are isolated examples, whereas we would like evidence that the pool of quantum-solvable questions is inexhaustible. Can we take inspiration from strongly correlated physics to write down a concrete ensemble of Hamiltonian simulation instances where there is a classically-hard observable? This would gather evidence for the sustained, broad utility of quantum simulation, and would also help us understand where and how quantum advantage arises.

Over in the computer science community, there has been a lot of work on oracle separations such as welded trees and forrelation, which should give us confidence in the abilities of quantum computers. Can we instantiate these oracles in a way that pragmatically remains classically hard? This is necessary in order to pass our earlier litmus test of being ready to run the quantum algorithm tomorrow.

In addition to Hamiltonian simulation, there are several other broad classes of quantum algorithms, including quantum algorithms for linear systems of equations and differential equations, variational quantum algorithms for machine learning, and quantum algorithms for optimization. These frameworks sometimes come with proofs of BQP-completeness.

The issue with these broad frameworks is that they often do not specify a distribution over inputs. Can we find novel ensembles of inputs to these frameworks which exhibit super-quadratic speedups? BQP-completeness shows that one has translated the notion of quantum computation into a different language, which allows one to embed an existing quantum algorithm such as Shor’s algorithm into your framework. But in order to discover a new quantum algorithm, you must find an ensemble of BQP computations which does not arise from Shor’s algorithm.

Table I claims that sampling tasks alone are not useful since they are not even quantumly repeatable. One may wonder if sampling tasks could be useful in some way. After all, classical Monte Carlo sampling algorithms are widely used in practice. However, applications of sampling typically use samples to extract meaningful information or specific features of the underlying distribution. For example, Monte Carlo sampling can be used to evaluate integrals in Bayesian inference and statistical physics. In contrast, samples obtained from random quantum circuits lack any discernible features. If a collection of quantum algorithms generated samples containing meaningful signals from which one could extract classically hard-to-compute values, those algorithms would effectively transition into the compute a value category.

Table I also claims that proofs of quantumness are not useful. This is not completely true—one potential application is generating certifiable randomness. However, such applications are generally cryptographic rather than computational in nature. Specifically, proofs of quantumness cannot help us solve problems or answer questions whose solutions we do not already know.

Finally, there are several exciting directions proposing applications of quantum technologies in sensing and metrology, communication, learning with quantum memory, and streaming. These are very interesting, and I hope that mankind’s second century of quantum mechanics brings forth all flavors of capabilities. However, the technological momentum is mostly focused on building quantum computers for the purpose of computational advantage, and so this is where breakthroughs will have the greatest immediate impact.

Don’t be too afraid

At the annual QIP conference, only a handful of papers out of hundreds each year attempt to advance new quantum algorithms. Given the stakes, why is this number so low? One common explanation is that quantum algorithm research is simply too difficult. Nevertheless, we have seen substantial progress in quantum algorithms in recent years. After an underwhelming lack of end-to-end proposals with the potential for utility between the years 2000 and 2020, Table I exhibits several breakthroughs from the past 5 years.

In between blind optimism and resigned pessimism, embracing a mission-driven mindset can propel our field forward. We should allow ourselves to adopt a more exploratory, scrappier approach: We can hunt for quantum advantages in yet-unstudied problems or subtle signals in the third decimal place. The bar for meaningful progress is lower than it might seem, and even incremental advances are valuable. Don’t be too afraid!

1. Quadratic speedups are widespread but will not form the basis of practical quantum advantage due to the overheads associated with quantum error-correction. ︎