Tensor network simulations challenge claims of quantum advantage...again!

Hot off the arXiv today: Efficient tensor network simulation of IBM's kicked Ising experiment

The authors report efficient classical simulations of the experiments by the IBM quantum computing team reported in Nature last week: Evidence for the utility of quantum computing before fault tolerance

What's going on here?

Tensor network methods are proving to be extremely powerful for computations related to quantum systems and large-scale neural networks. They work best for simulations of 1-dimensional or tree-like quantum systems (corresponding to the special case of matrix product states). Higher-dimensional systems or those with long range coupling containing looped paths, however, incur increasing overheads.

The Eagle quantum processor used in IBM's recent experiments is based on a two-dimensional network of qubits on a "heavy hexagon" grid. Thus, even though it is two-dimensional (harder for tensor network methods), its loops are longer than that of a more compact square lattice. The time required to traverse a single loop is comparable to the circuit depths probed in the experiment, meaning that by applying some clever factorization tricks the dynamics can be reproduced by efficiently-simulable tree-like tensor networks!

 

This is not the first time tensor networks have challenged claims of supremacy - they have also been used to simulate Google's original quantum supremacy experiments. What is particularly striking here is that the time between the publication of the quantum experiment and publication of the classical reproduction has dropped from years to weeks!

Here are some libraries for trying out tensor network simulations of quantum systems:

tensorcircuit: Python library developed by Tencent Quantum Lab - can handle shallow circuits involving hundreds of qubits.

ITensorNetworks: Julia library developed by the Flatiron Institute, which was used to reproduce the IBM experiments.

For theorists, getting familiar with these simulation tools that can also be applied to other important areas (such as large-scale machine learning or numerical simulations) seems to be a better use of time than getting to grips with the intricacies of ever-changing device-specific error models and quantum error mitigation schemes!

The localization landscape

Localization of waves due to destructive interference in disordered media - Anderson localization - has been a subject of intense investigation for more than 50 years. The original paper has now been cited more than 15,000 times according to Google Scholar. Being a property of linear, non-interacting Hamiltonians subjected to a random potential, one might think that everything there is to know about this problem would have already been studied to death a long time ago, with current work focusing on understanding peculiarities arising under special circumstances.

Delightfully, this is not the case! Back in February, this preprint caught my attention due to its keywords of many-body localization and persistent homology. Specifically, the authors have used persistent homology to characterize the shape of the "localization landscape" of a many-body Hamiltonian. 

What is the localization landscape?

The localization landscape was first proposed by Filoche and Mayboroda in an article in PNAS which, despite its broad applicability to understanding wave transport in a variety of settings (condensed matter, photonics, acoustics), did not attract as much interest as other arguably more specialized areas such as non-Hermitian systems or topological edge states. In short, the localization landscape u of a Hamiltonian $\mathcal{H}$ satisfying certain properties is the solution of the linear equation

$$\mathcal{H} u = \mathcal{1},$$

where $\mathcal{1}$ is a vector with all elements equal to 1. u corresponds to the steady-state response of the medium to a uniformly-distributed source.

Left: The localization landscape of a disordered two-dimensional wave medium. Right: Five lowest energy eigenstates of the Hamiltonian, which are localized to distinct peaks of the landscape bounded by lines of small $u$ (red). For more details, read the paper!

Remarkably, it can be shown that $u$ bounds the spatial extend of the low energy eigenmodes of $\mathcal{H}$. Thus, instead of solving the eigenvalue problem and plotting its low energy modes individually to find out where they are localized, plotting $u$ alone is enough to find all the effective low-energy valleys in a medium. Moreover, as a solution to a linear system of equations, $u$ is easier to obtain than the eigenstates themselves. A more rigorous discussion (including the properties that must be satisfied by $\mathcal{H}$ can be found in the PNAS article, which is a pleasant and accessible read.

Interest is now growing in localization landscapes, thanks to recent generalizations that can bound the spatial extent of modes residing in the middle of the energy spectrum, eigenvectors of real symmetric matrices and modes of many-body interacting quantum systems. The latter remarkably shows that useful landscape functions are not limited to low-dimensional wave media, but can also bound the spreading of wavefunctions in the high-dimensional Fock space of many-body quantum systems.

A natural question that arises from these recent works is whether the localization landscape might have some potential applications in the context of quantum computing and noisy intermediate-scale quantum (NISQ) processors. For example, finding the ground state of a generic many-body Hamiltonian is a computationally challenging problem, and methods for NISQ devices such as the variational quantum eigensolver may fail to converge due to the presence of vanishing gradients or sub-optimal local minima. 

Can the localization landscape offer an easier, more hardware-efficient way to sample from low-energy solutions of a hard-to-solve Hamiltonian? Watch this space to find out!

Reading the right papers

Students often find it particularly hard to tell which papers are worth an in-depth reading, which can be skimmed, and which are not essential to the current research project. Since this is something that is usually only learned through experience, examples can be helpful for building intuition.

Consider the first paper from my PhD research, Pseudospin and nonlinear conical diffraction in Lieb lattices, published in Physical Review A. With the benefit of hindsight, this turned out to be a Good Paper, with multiple experimental groups exploring some of the ideas in the following years. Why did it have an impact?

The research project didn't start by reading a bunch of papers and getting a new idea. The idea arose from talking to people - experimental collaborators, and one of the eventual co-authors (Omri), who had recently finished his PhD on the theory of wave propagation in graphene-like honeycomb photonic lattices. 

I was asked to see whether any of the ideas in his thesis could be feasibly investigated by our experimental collaborators. Honeycomb lattices being hard to do in their setup at the time, they wanted to know whether similar phenomena might be observable in a square lattice. Similar to how one can remove a period-doubled lattice from the triangular lattice to create a honeycomb lattice, removing sites from an ordinary square lattice yields a face-centred square lattice with intersecting bands. Great!

As is so often the case in research, we were not the first to have this idea, and actually in the preceding few years several groups had been exploring the properties of this lattice, motivated by huge interest in the electronic properties of graphene (Refs. [7,8,10,11,12,13] in the paper). These works were all published in the Physical Review, not "high impact" venues such as Nature / PRL, probably because referees thought it would be difficult to reproduce this model in an experiment. Being background material, an in-depth reading of all these papers was not required - we just needed to know roughly what they did and how they did it to understand how novel our results were.

In these papers we not only found the now commonly-used name for this lattice (the Lieb lattice), but also learned about how its properties were of interest in the context of cold atoms / BECs and electronic properties of materials. Lucky for us, we could not find any papers studying this lattice from the point of view of photonics, meaning that we had something novel! But on the other hand, we clearly couldn't just take these existing results (based on tight binding models) and do exactly the same using a "photonic" tight binding model without our work ending up being merely incremental and forgettable. Therefore we considered a few photonics-specific extensions:

(1) Wave propagation dynamics in the nonlinear regime, translating the analysis in one of Omri's recent papers (Ref. [11]) to the Lieb lattice setting. This one I had to read and re-read in detail to fully understand the analytical and numerical simulation tools used.

(2) Understanding the coupling between the different angular momentum degrees of freedom in our system. This similarly involved an extension of previous results by others for the honeycomb lattice (Ref. [18]) to the Lieb lattice setting. We also had to carefully read and understand this paper.

(3) Photonics-specific simulations not limited to a tight binding approximation and using experimentally-feasible parameters similar to those used in our collaborators' recent work (Ref. [26]).

In summary:

• Talk to experts early on to find out what the real important problems are and whether they have any that you are in a position to solve.
• Once you have an approximate solution or plan of attack, you need to check the literature to understand its importance and relevance to other work. At this stage you will often encounter papers with ideas very similar to yours.
• Identify your niche and expand on the novel points of your work, usually building on a few specific related papers that need to be carefully read and understood.
• It is usually easier to first solve a specific problem a single expert is having, and then figure out how your solution generalizes. The reverse approach - solving a problem in generality before considering specific examples - should only be attempted with extreme caution.

Doing literature reviews the smart way

Despite literature surveys being a key component of research, strategies for reviewing the scientific literature and identifying promising avenues of research are rarely included in graduate student coursework. This means that students may be unaware of more powerful tools that are available.

It is useful to have a tiered search strategy, starting with resources aimed at a broad audience, for example technical magazines such as Optics & Photonics News, to identify interesting or promising directions to study in more detail. While wikipedia is a popular first choice, peer-reviewed alternatives such as Scholarpedia provide more reliable and trustworthy articles written by known experts.

Google Scholar is perhaps the most popular scholarly search engine, but its limitations mean it is most useful for exploring papers on highly specific lines of research, mainly by following citation trains and highly-cited papers. Subscription-based search engines such as Web of Science are usually available under university subscriptions and give much more powerful tools for exploring a research area and seeing the bigger picture, such as the ability to filter search results by journal or author affiliations and visualise how publication trends are evolving over time using citation reports

Thanks to covid, many academic talks can now be viewed online. These are a great alternative to reading the papers themselves, particularly because the speaker may reveal insights that didn't end up in the journal article. One should keep in mind differences between workshops and larger conferences - target audience, breadth and depth of individual talks and the programme as a whole, and sometimes the candour of the speakers, particularly if the talk will be made available online. This means that in-person conference attendance is still highly valuable, because speakers may be more willing to share unpublished work and future research ideas during smaller more informal discussions. Talking to the right person can save hours of time figuring out what the key references are!

The volume of publications in an area may shape your research strategy. If a given keyword has hundreds or thousands of articles coming out each year, it's usually a sign that you need to narrow your focus to find a niche in which you can shine. Publications often follow a hype cycle, that is, an initial surge of interest leading to a transient peak in activity, followed by a more stable plateau as the field matures. Sometimes a line ends up being infeasible, leading to interest dying off before such a plateau can form.

It is important to emphasize the number of publications in an area should not be used to judge whether a field is worthwhile to study. For example, one researcher might see a booming field and be put off, desiring to work in a smaller area with a better potential for growth. A short peak of activity followed by little interest may suggest a research line has a difficult problem that nobody knows how to solve, offering an opportunity for you to make your mark.

Does artificial intelligence have a place in reviewing the literature and deciding on promising lines of research? Yes and no. Artificial intelligence is more than just large language models and chatbots, encompassing a variety of other machine learning-based tools for enhancing productivity, for example by helping to analyse and visualise citation networks. Some experimental examples of these network analysis tools are available on arXiv through arXivlabs and are worth a try - even if their capabilities are limited or inaccessible today (e.g. requiring a subscription), in the coming years the best ones will become more widely available via university-wide subscriptions, similar to the growth of collaborative paper-writing tools such as Overleaf.

And what about large language models? In my opinion, it's best to avoid them when carrying out literature reviews. Language models are trained to favour fluency over accuracy, so rather than generating new knowledge they are better used for performing tasks where the end-user can verify the output. Even when asked to analyze specific papers, you can't be sure that the model missed or misunderstood an important point, for example when jargon used within a research area differs from the commonly-understood meaning of a word. And even if (or when) these issues are solved by new and improved models, at the end of the day large language models are designed to spit out probable-sounding sequence of tokens. On the other hand, scientific breakthroughs often come about through the pursuit of unlikely or unexpected avenues of investigation.

Finally, one should not read too much. Too much time spent reading what other people have done not only takes time away from your own research, but it can also sap your creativity and ability to pursue directions away from the groupthink. Richard Hamming explained this eloquently in famous lecture "You and Your Research" he gave at Bell Labs, available both as a text transcript and a video recording. I highly recommend reading or watching!

In summary:

1. You should use a variety of sources, search engines, and media types
2. Remember every source and search engine has a bias
3. Aggregated statistics are just as important as individual papers
4. Try emerging AI-powered search & visualization tools
5. Don't read too much!