CODA

Compressed Optimization of Device Architecture (CODA) is a method of both finding good operating points within a device, while simultaneously quantifying how easily tunable a given device is.

Arxiv Post

The current version of the manuscript can be found here.

Referee reports

On October 27, 2014, Nature Communications rejected the CODA manuscript, with the following reviews.

Reviewer #1

Dear Editor,

please find below my report for

"Compressed optimization of device architectures" by Dr Gamble et.al Nature Communications manuscript NCOMMS-14-16172-T

First let me begin this review with a brief overview of the paper and its results. The focus of the paper is on an optimization protocol to control static voltage levels to ensure a correct occupation number in the correct quantum dot. Overall this manuscript is quite well written but I am not sure it is appropriate for Nature Communications. First, the optimization protocol seems to me to be very specific and cannot be the only problem in control needed for assembling such a quantum dot quantum computer.

Maybe we should publish instead in a more focussed journal, like PR applied?

Further the simulations of the single double well shows that their protocol can be useful at informing design decisions for the basic quantum dot array. But again, I'm not sure of the relevance of this when demonstrated with a single quantum dot. Surely this can be done by hand with detailed CAD modelling? The assumption of the entire work seems to be the claim that this approach is scalable (to the relevant levels of a large scale computer). But aside from comments on the second page about how their modification of the optimization problems reduces an otherwise NP-Hard problem to something efficient (I assume they mean polynomially efficient in some parameter, but they don't say) they actually don't seem to demonstrate a convincing level of scalability.

From this, we obviously need to show the progression between the unit cell optimization and the larger arrays more clearly.

Why can't they show large scale simulations? is a restriction in the optimization protocol? or is it too hard to accurately simulate the physics that their characterization and optimization protocol will work on.

Is there something we can do here? Maybe mock up a simplified geometry, but a much larger system, in COMSOL?

If Nature communications is appropriate, they need to make a much better argument that this technique will be appropriate for a computer (not simply designing small scale devices).

The design discussions in the paper are restricted to a single quantum dot and applying 3 different electrode configurations and testing them. I noticed that they don't argue in the paper that this technique can tell them what the best configuration is beforehand. They still have to design (through intuition or something else) the initial electrode configurations. All their protocol does is effectively compare them after they are done. For the 8-qubit device they don't seem to even attempt a design optimization. Again, the physical layout is already fixed.

This seems like a common comment between the two referees. I think that we should try to do some sort of geometry optimization as a demo.

Next in the 8-qubit optimization simulations, they have a target dot on the right with some target optimization number and the series of four plots illustrating the voltage potentials needed to ensure some fixed error rate. However, either I missed it (or they didn't address it). How does this protocol effect the occupation of the other 7 quantum dots? Are they assuming some fixed occupation number and ensuring that these are matched to the same error rate? or are they only examining the target dot?

Both of the referees missed that we are targeting the charge configuration for all the dots. This needs to be made clearer.

The paper as written is quite short and obviously was not initially intended for Nature Communications (as the formatting is incorrect). It is written in letter style rather than the article style. In the article format significantly details could be added. However in its current form I am not sure this paper is appropriate for Nature communications as the problem they are solving is very specific.

Probably lengthening the paper and going with a different journal would be best...

Reviewer #2

This manuscript covers a very important topic: more efficient ways to design gates and tune voltages for multiple quantum dot devices. There is no doubt that an efficient method for this problem is of interest to the quantum engineering community. In their introduction, the authors lay out an ambitious program for employing numeric optimization to find a device design in which local tuning of gates to trap electrons and allow tunneling rates of appropriate magnitude using as small a number of gate voltages per gate as possible. Sounds good!

Unfortunately, the results the authors present seem like an early stage in this program. It is an interesting step, but in my mind is of little utility at this stage.

• The problem being tackled is not nearly as simple as the present work lays out. The response of electrons

to voltage is not linear with respect to voltage, nor is it linear with respect to the potential created by that voltage. In fact, the numeric solution for regions of charge stability is a challenging problem, and if I understand correctly such numeric solutions are required for every step in the optimization process for every control variation delta_c. Screened Poisson-Schroedinger is notoriously insufficient for modeling devices in which trapped, discrete charges are the target; they must be combined with molecular modeling techniques to have any reliability. In particular, it is confusing that "electron number" is the continuous target in their search metric, since in reality charge is a discretely measured number and there are large regions in voltage space of charge stability. The metric being employed by the authors is in fact the height of the potential at a particular region, which is being related to charge via Eq. (3) of the supplemental information; this is not a sufficiently physical metric in my mind, and would work poorly if experimental data were being employed for the optimization. Moreover, if the authors are looking at regions of voltage space in which electrons are added, then they absolutely must concern themselves with *tunnel rates*, since in reality charge stability near charge transition regions depend critically on how long one is willing to wait for an electron to tunnel in. The authors approach this by looking at inter-dot tunnel rates using WKB, but for charge stability one should look at tunnel rates to a bath, bath chemical potential, etc. all at once. I have no doubt that the authors are aware of these issues, and I have little doubt that their response is that you have to simplify the problem sufficiently to start somewhere in such problems. Indeed you do, but the problem with this work as I read it is that it is just a start, and far from being close enough to reality to inform experiment meaningfully.

I'm not sure what to do about this. Maybe we should be more clear about the drastic approximations used in our model, but emphasize that the focus is on the reduction of a terrible, non-linear system to one that is easy to solve. Also, maybe showing how to navigate a discrete honeycomb plot would be good? Overall, I think taking a more "simulating the experimental process" route would be better. For instance, we could show CODA navigating the charge-stability diagram, hitting a wall in tunnel coupling, etc.

• The numeric algorithm (CODA) is doing very little for design. The gate designs in this paper are all being

generated by hand, and the "working point" (the beginning of step one in their CODA procedure) must be found by hand as well. The only thing CODA offers is a curve (as in Fig. 2c, 3g, 3h) which shows how much the error with respect to a target changes with the L1 norm. Actually, this is quite an abstract curve and I am still not clear, after a couple readings of the paper, how to interpret this plot. I recognize that the trace is being generated by changing the weighting factor alpha, and that this trades off accuracy vs. (roughly) number of gates needed to control the desired target, but it is not clear what makes one such curve "better" than another. I suppose it is simply how quickly the accuracy reduces with respect to L1 norm, but this captures accuracy vs. total (L1) voltage rather than what we really care about, which is accuracy vs. locality/cross-talk. Surely there is a better way to quantify this that makes the bottom line of this paper clearer.

We need to use it to optimize something. Distilling the curves down to a metric would be very good... any thoughts?

• The example targets given are too simple. The importance of this manuscript's goal is the ability to use

computers to help design and tune large arrays of dots. But all examples deal with only pairs of dots, even in the more complex

• looking* device of figure 2. Unless I missed it, what would be

important to me would not just be the number of gates needed to affect the charge of the rightmost dot, but the ability to control this rightmost dot without adversely affecting the charge in the other 7 dots. It seems like *every target should involve every dot*, and it is not clear that the authors have done this yet. This is critical though. It is not interesting that I can get good charge control in the rightmost dot with four gates, if those same four gates also strongly affect the charge of next dot over with the help of the next four gates, and these affect the next dot over with the help of the next four gates, etc. If there is this much crosstalk, then we'll always be using every gate for everything we do, and the whole program of seeking sparsity was never useful in the first place.

We did this, and both referees missed it! That means we must not have been very clear...

• Speaking of sparsity, the authors use the word "compressed" in their title and algorithm name, and they

indicate that this algorithm is somehow using compressed sensing. In reality, it is not. Compressed sensing *exploits* sparsity to find a solution; the present algorithm *enforces* or *minimizes* sparsity. As their own curves show, for most devices the "best solutions" are not sparse at all; the authors are forcing sparse solutions at the trade-off of accuracy by manually putting it into their optimization metric. This is not what compressed sensing is about. The authors use the words "related to" in order to not be imprecise, but the emphasis on compressed sensing in the introduction feels a little like a gratuitous drop of a "hot topic."

We should probably emphasize that locality is the goal, and sparsity is a convenient way to achieve it.

I am certain I am not saying anything surprising to the authors, and I suspect that they are fully aware that their notion of device architecture optimization is far from complete. I suspect we all agree that the assumptions presented and the use of Eq. (2) is just one small step in a much larger effort. The question on the table now is whether this small step should be published, and whether it should be published in Nature Communications in the form of the present manuscript. In my opinion, in the present form, no. For this paper to be beneficial, it should be more technical. The exact equations used to calculate error and WKB rates should be more explicit. The algorithm employed for convex optimization should be spelled out. The limitations and future directions of the method should be discussed at length. The amount of computing time employed and the prospects for doing this procedure with more complex simulation models or even with experimental data should be quantified. In short, if this is to be a publication at all it should be detailed science spelled out for detail-oriented scientists, in a journal appropriate for such discourse, because it will only be useful if its audience is able to reproduce it and build upon it. As written, it is not this; it is a promise of a useful numeric optimization routine without enough substance to easily reproduce or build upon, and certainly not enough to actually use to invest in new device formulae. I was full of hope when reading the abstract, and then disappointed by how little distance into the large problem space the manuscript reports. I doubt the authors (or the editors) would want this reaction from other readers.

I think the referee has a point that more details and fleshing out some of the simulations will make the paper as a whole much more compelling. The right place for it isn't nature comms; I'd say PR applied, after the additional simulations are completed.