ArXiv: 2311.17894

🎯 Pitch

Shooting an electron beam at the carbon atom next to a silicon dopant in graphene makes it jump with 50% successβ€”double the rate of any other heuristic approach. The authors trained a neural network on STEM-collected atomic maneuvers to predict these transition probabilities, then used the learned model to autonomously steer a silicon atom along shortest-path routes to target locations.

1. Executive Summary

This paper introduces a machine learning pipeline to estimate the transition dynamics of a single silicon dopant atom on a graphene lattice when stimulated by the electron beam of a scanning transmission electron microscope (STEM). The approach processes STEM-collected images through atomic alignment and data filtering to produce symbolic representations, then trains a neural network to predict transition probabilities decomposed into a total transition rate and a categorical distribution over neighboring carbon sites (parameterized as an exponential cumulative distribution function for whether any move occurs and a softmax over which neighbor is chosen if it does). The learned on-neighbor beam placement strategy achieves a 50.0% transition success rate (95% CI 0.246 to 0.754) with a five-second dwell time at 90 pA beam current, outperforming heuristic alternatives that fall below 25%, and is demonstrated to autonomously steer the dopant along shortest-path trajectories to pre-specified target positions. A synthetic evaluation framework confirms that the model converges to accurate rate estimates once hundreds of positive transitions are available, establishing that data-driven transition modeling enables automated atomic manipulation only when sufficient positive-transition examples have been collected and the system is restricted to the single-dopant, pristine-lattice setting studied.

2. Context and Motivation

The Core Problem: Atomic Manipulation Lacks Quantified, Reliable Transition Dynamics

The fundamental question this paper tackles is deceptively practical: if you want to move a single silicon atom across a graphene lattice by shooting electrons at it, where exactly should you aim the beam and for how long to maximize your chances of success? Prior to this work, the microscopy community operated on physical intuition β€” specifically, the assumption that placing the electron beam directly on a neighboring carbon atom is the optimal strategy β€” but this intuition had never been systematically quantified, verified, or characterized across different configurations. The paper's central gap identification is that the transition dynamics of dopant atoms under electron beam stimulation have been studied only anecdotally, without a data-driven measurement of the actual probability distribution governing atomic motion.

This gap matters because it blocks the transition from manual, human-guided atomic manipulation to fully automated, high-throughput atomic fabrication. A human operator can afford to experiment with beam positions, watch what happens, and adjust; an automated controller needs an explicit probability model to make decisions. The paper makes this distinction explicit in the problem description: "To date, the microscopy community has relied on heuristic estimates for these transition dynamics, with anecdotal evidence of their accurateness." Without quantified transition probabilities, there is no principled way to choose beam placement, no way to predict how long a manipulation sequence will take, and no way to optimize trajectories for efficiency.

Why Automated Atomic Manipulation Matters

The paper situates its work within a broader vision of direct atomic construction β€” the ability to assemble matter atom by atom β€” and argues that STEM-based manipulation is a uniquely promising but underdeveloped pathway toward that vision. The stakes are framed in both practical and fundamental terms:

Practical applications (Section 2 and Section 7): The paper connects its work to three concrete technology areas:

  • Solid-state quantum computers: Fabrication of phosphorus and other dopant atoms in silicon qubits requires precise placement of individual atoms. The paper cites this as "perhaps the application that has attracted the most interest" in tip-induced atomic motion.
  • Nanopore fabrication for protein sequencing: Precise atomic-scale holes in materials enable single-molecule sensing.
  • Molecule screening platforms and quantum communication/sensing devices: These all require "precision and throughput" in atomic fabrication that manual control cannot provide.

Fundamental capability (Section 7, citing Feynman): The paper invokes Feynman's final blackboard message β€” "What I cannot create, I do not understand" β€” to frame atomic manipulation as a scientific necessity, not just an engineering goal. Understanding matter at the deepest level requires the ability to build it from scratch.

The throughput bottleneck: The paper emphasizes a critical mismatch between machine capability and human speed. The characteristic timescale of human-operated experiments "vastly exceeds the intrinsic latency of the electron microscope, for which hundreds of fabrication steps per second should be possible." A human operator placing one beam position at a time, observing the result, and then deciding the next position operates on the timescale of seconds to minutes per step; the microscope itself could operate orders of magnitude faster if automated. This throughput gap β€” not just precision or reproducibility β€” is what makes manual control fundamentally insufficient for real applications.

Prior Approaches and Their Limitations

The paper traces a history of atomic manipulation from its origins to the current state-of-the-art, identifying specific shortcomings at each stage:

STM-based manipulation (Stroscio and Eigler, 1991): The landmark achievement of positioning individual Xenon atoms on a surface to form the IBM logo established the feasibility of atomic-scale construction. However, STM-based manipulation has a fundamental physical limitation: it works only on metallic or conducting surfaces, because the scanning tunneling microscope requires a conductive substrate. This excludes broad classes of materials, including the graphene-on-insulator systems that are of growing interest for 2D materials research and device fabrication.

STEM-based manipulation β€” the haphazard era: The electron beam of a STEM can manipulate atoms embedded within several-layer-thick specimens, including non-conducting materials. However, prior to this work, STEM manipulation was described as "a rather haphazard and unpredictable process." The paper identifies three specific modes of prior STEM operation, each with critical weaknesses:

  1. Raster scanning: The most common approach, where the electron beam scans a rectangular pattern over a selected field of view. The problem is that "the electron dose tends to be concentrated non-uniformly on one side of the image," meaning the beam is not deliberately positioned to influence specific atoms. This is essentially an uncontrolled exposure β€” sometimes something interesting happens, but it cannot be directed.

  2. Manual beam positioning by a human operator: More sophisticated experiments involve a human manually positioning the beam. However, the paper states this "kind of motion is unpredictable and unreliable, and useful statistics are challenging (if not impossible) to glean from experiments conducted in this manner." Each attempt is a one-off, conditions vary between attempts, and there is no systematic record of beam positions, outcomes, and probabilities.

  3. Direct-write beam patterning without atomic awareness: Some experiments control the electron beam in non-standard trajectories for direct-write patterning, but "with the critical point that the atomic landscape (i.e., position of atoms) is not considered." The beam draws patterns without knowledge of where atoms actually are, so it cannot target specific atomic sites. This is like trying to rearrange furniture by moving objects in a dark room β€” you might accomplish something, but not with precision or intent.

The heuristic that needed testing: The paper identifies a specific piece of received wisdom in the community: the physically intuitive assumption that "the optimal beam position is directly on a neighboring atom." This assumption arises from the dominant damage mechanism being "knock-on" processes β€” momentum transfer from the electron beam to atoms, which would be maximized when the beam is centered on the target atom. However, the paper points out several reasons this heuristic might be wrong or incomplete:

  • Damage mechanisms are "dictated by more than one process" β€” ionization and sputtering may also be occurring, which have different spatial dependencies.
  • The knock-on intuition "is mostly valid only for a direct Si substitution (i.e., 3-fold coordinated silicon)." For other configurations β€” different bonding environments, different numbers of neighbors, non-pristine lattices β€” "the optimal beam position for causing a transition event is not clear."

In other words, the community had a plausible but untested hypothesis that happened to work some of the time. What was missing was a systematic, quantitative measurement of transition probability as a function of beam position.

The machine learning proposal β€” unrealized: In 2016, Kalinin et al. proposed that combining machine learning with electron beam manipulation could become "a third paradigm for direct atomic construction." This paper is, in a direct sense, the implementation and validation of that proposal. The 2016 proposal recognized that the complexity of beam-induced dynamics β€” multiple interacting physical mechanisms, probabilistic outcomes, spatial dependence β€” makes it well-suited to data-driven modeling. But until this work, no one had actually collected the necessary data, built the pipeline to process it into training signals, and used the resulting model to close the control loop.

Conflicting or Insufficient Evidence

The paper's motivation also draws from a more subtle gap: the absence of any quantitative measurement of transition probabilities in the literature. Prior work (Dyck et al., 2017; Susi et al., 2017a,b; Tripathi et al., 2018) had demonstrated that single-atom manipulation in graphene is possible β€” atoms can be made to move, and with patience and skill, they can be guided to desired locations. But possibility is not the same as predictability. The paper argues that for automation, you need more than a demonstration; you need a probability distribution:

P(Sβ€²βˆ£s0,a)P(S' \mid s_0, a)

where Sβ€²S' is the next position of the dopant, s0s_0 is its current position, and aa specifies the beam position and dwell time. Prior work had never estimated this distribution, much less validated its accuracy or used it for closed-loop control.

How This Paper Positions Itself

The paper positions itself not as introducing a fundamentally new physical mechanism or microscope capability, but as replacing heuristic human judgment with a quantified, data-driven model that enables automation. This is a classic "from art to science" transition: the existing capability (moving dopants with a STEM) is taken as given, and the contribution is making it systematic, measurable, and automatable.

The paper's framing emphasizes three novel elements:

1. The data-centric methodology (Section 4): Rather than proposing a theoretical model of beam-induced transitions based on first-principles physics (which would need to account for multiple interacting damage mechanisms, thermal effects, and quantum-level interactions), the paper takes an empirical approach: collect many examples of beam positions and their outcomes, process them into a consistent format, and learn the transition function from the data. This is particularly appropriate because the underlying physics is complex and not fully understood β€” exactly the regime where machine learning excels.

2. The end-to-end pipeline from raw data to control (Figure 2): The paper's contribution is not just a neural network architecture but the entire sequence of steps needed to go from microscope images to a working controller: atomic alignment to correct for specimen drift, data filtering to identify valid transitions, data augmentation to enforce physical symmetries (rotation and reflection invariance), a parametric model respecting monotonicity of transition probability with dwell time, and ensemble distillation for robustness.

3. The validation through control (Section 5), not just prediction accuracy: The paper explicitly acknowledges that "we do not have ground-truth data for the learned transition probabilities." Rather than claiming accuracy of the probability estimates themselves, the paper validates its model by using it for control β€” if the learned policy successfully moves dopants to target positions, it must have captured something real about the underlying dynamics, even if the exact probability values cannot be independently verified.

The paper is also careful to bound its scope: "The scenario we considered in this work is somewhat idealized: we limit ourselves to single dopant and 3-way lattices." This is not presented as a limitation to be overcome later, but as a deliberate choice: the simplest scientifically interesting setting that allows rigorous validation before extending to more complex configurations (multiple dopants, 4-fold coordinated graphene, lattices with defects). The paper is establishing a methodological foundation, not claiming to solve the general atomic manipulation problem.

The Tension Between Manual Expertise and Automation

An undercurrent in the paper's motivation is the tension between the deep tacit knowledge of expert microscopists and the requirements of automated systems. An expert human operator can recognize subtle image features, adjust beam position based on visual feedback, and develop an intuitive sense of what works. But this expertise is:

  • Non-transferable: It exists in the minds of a few researchers and cannot be easily shared or replicated.
  • Non-scalable: One human can control one microscope at a time, at human speed.
  • Non-quantifiable: The expert "knows" where to put the beam, but cannot produce a probability distribution justifying that choice.

The paper's approach can be read as an attempt to extract this tacit knowledge into an explicit, computable form. The data collected from the microscope β€” beam positions, dwell times, and resulting atom positions β€” is essentially a record of physical "experiments" that encode the transition dynamics. The neural network learns to approximate whatever function the expert microscopist has implicitly internalized, but in a form that can be queried automatically, shared with other systems, and used for optimization.

This also explains why the paper places such emphasis on the data filtering and alignment pipeline (Section 4.2-4.3). The raw data from a microscope is messy: atoms are hard to detect reliably, the sample drifts during imaging, and not every recorded transition is a clean single-hop between valid lattice sites. An expert human filters out these issues unconsciously; an automated system needs explicit steps to discard bad data and align the rest. The fact that approximately 80% of the initial data was discarded during filtering (6,754 examples β†’ 1,953 usable examples) underscores how much tacit quality control the system must replicate.

3. Technical Approach

3.1 Reader Orientation

The system being built is a data-to-control pipeline that takes raw microscope images of a silicon dopant on graphene, processes them into clean symbolic representations of atomic positions and beam parameters, trains a neural network to predict the probability that a given beam placement and dwell time will cause the dopant to hop to a specific neighboring carbon site, and then uses those learned probabilities to automatically steer the dopant along shortest-path trajectories to any desired target location. The problem it solves is replacing heuristic human judgment about where to aim the electron beam with an explicit, quantified probability model β€” taking atomic manipulation from an art practiced by a few experts to a repeatable automated process, without requiring any first-principles physical modeling of the complex beam-matter interactions.

3.2 Big-Picture Architecture (Diagram in Words)

The pipeline has four major stages, illustrated in Figure 2:

  1. Data acquisition and image processing (Section 4.1): A STEM repeatedly images a graphene sheet with a single silicon dopant, fires the electron beam at a sampled position for a sampled dwell time, and re-images the result. Each such trial produces a before-and-after pair of images plus a record of beam parameters.

  2. Atomic alignment (Section 4.2): A convolutional neural network corrects for physical movement (specimen drift) between successive images by predicting a two-dimensional shift vector that brings the lattice positions into register. This alignment is applied iteratively for precision and is critical because misalignment would corrupt the training signal.

  3. Data filtering, augmentation, and standardization (Section 4.3): The aligned images are processed through atom detection to extract atomic coordinates. Each trial is then checked against validity criteria (exactly one dopant before and after, exactly three neighbors in both states, consistent lattice geometry), and invalid trials are discarded. Valid examples are rotated and reflected to enforce physical symmetries, and beam positions are translated to a dopant-centric coordinate frame.

  4. Transition dynamics learning and controller deployment (Sections 4.4 and 5): A neural network ensemble is trained on the filtered data to predict transition probabilities as a continuous rate function over beam positions. The learned model's optimal beam placement (maximizing transition probability) is extracted and used by a greedy controller that iteratively drives the dopant toward a goal position.

3.3 Roadmap for the Deep Dive

  • First, the data collection protocol β€” exactly how the microscope is operated to generate informative training examples, what parameters are varied, and why imaging itself is a confounding factor that must be minimized.
  • Second, the atomic alignment network β€” the architecture, training procedure, and why iterative application is essential for drift correction quality, along with why simpler alternatives (cross-correlation, ICP) fail.
  • Third, the data filtering and augmentation pipeline β€” what validity checks are applied, what fraction of data survives, and how rotation/reflection augmentation encodes physical symmetries into the training set.
  • Fourth, the transition dynamics model itself β€” the decomposition into total rate and categorical neighbor distribution, the exponential CDF form that enforces monotonicity in dwell time, the loss functions, and the ensemble distillation procedure.
  • Fifth, the synthetic evaluation framework and control strategies β€” how simulated data validates the learning algorithm, how regret is defined as a control-relevant metric distinct from MSE, and what beam-placement strategies are compared experimentally.

3.4 Detailed, Sentence-Based Technical Breakdown

This is primarily a data-centric methodology paper whose core idea is that a neural network trained on systematically collected STEM observations can learn the transition probability function of a dopant atom well enough to enable fully automated control, without requiring any physical modeling of the underlying beam-matter interaction mechanisms.

Data Collection Protocol

The goal of data collection is to generate a dataset of (beam position, dwell time) β†’ (did the dopant move, and if so, to which neighbor?) examples that span the relevant input space with sufficient density to learn a continuous probability function. The protocol is designed to be executed automatically via a Python API controlling a Nion UltraSTEM 100 microscope.

Step-by-step procedure. Each data collection trial follows a fixed four-step cycle (Section 4.1):

  1. Acquire an initial image of the graphene with a field of view of 3 nm centered on the dopant. This image serves as the "before" state.

  2. Sample a beam position uniformly within a 2.84 Γ… radius of the dopant atom. This radius is chosen to be the cumulative length of two carbon-carbon bonds, ensuring that the sampled positions cover the region containing the dopant and all three of its immediate carbon neighbors. The sampling is uniform in Cartesian coordinates within the circular region.

  3. Focus the electron beam at the sampled position for a dwell time drawn from a distribution typically ranging from 1 to 10 seconds. The beam current is held at a nominal 90 pA throughout. The paper displays the histogram of dwell times and the spatial distribution of beam positions in Figure 3 (top row, left and center panels, respectively).

  4. Acquire a final image of the graphene to serve as the "after" state.

A critical design constraint acknowledged explicitly in the paper: image acquisition itself uses the same electron beam and can therefore cause transitions. To mitigate this confounding effect, the imaging electron dose is minimized to make it as unlikely as possible that the imaging step β€” rather than the deliberate beam-dwell step β€” induces the transition. This creates an inherent trade-off between image quality (more dose = clearer atom detection) and measurement validity (more dose = contamination of the training signal).

Why collect multiple samples at the same beam position? The paper notes that "it is important to gather multiple samples using the same beam position and dwell time, as transitions are probabilistic." A single observation of success or failure at a given beam position provides very little information about the underlying probability; multiple trials are needed to estimate the rate. The uniform random sampling over the 2.84 Γ… disk ensures that over many trials, the beam positions visited will cover the space with reasonable density, and some positions will be revisited by chance, providing repeated measurements.

Real-time atomic coordinate detection. For the beam to be placed at a known position relative to the dopant, the atomic coordinates must be known with high confidence in close to real time. The paper states this is "addressed by using deep ensemble neural networks to identify the atomic species and positions both quickly and reliably," citing Ghosh et al. (2021). This real-time detection runs in the control loop during data collection β€” it is not the same as the offline processing that occurs later in the pipeline.

Scale of data collection. The initial dataset consisted of 6,754 examples (trials), each representing one beam pulse and its observed outcome. After filtering (Section 4.3), 1,953 examples remained β€” approximately 29% of the raw data. The paper does not report the total wall-clock time for this collection, but given dwell times of 1–10 seconds per trial plus imaging overhead, it is on the order of several hours of continuous microscope operation.

Atomic Alignment via Convolutional Neural Network

The problem: specimen drift between images. Between the "before" and "after" image acquisitions, the graphene sheet may physically move β€” a phenomenon called specimen drift. Additionally, the electron beam can cause warping aberrations. If uncorrected, this drift means that an atom at pixel coordinates (x, y) in the first image is not at those same coordinates in the second image, even if it has not hopped. Any downstream analysis that compares "before" and "after" atomic positions would misinterpret physical drift as atomic motion, corrupting the transition labels.

Why classical approaches fail. The paper considered two standard solutions and rejected both:

  • Cross-correlation alignment: Taking the cross-correlation between the two scans and estimating drift as the arg max of this function. This fails because "images of this system are generally dominated by the very bright silicon dopants" β€” the silicon atom scatters electrons much more strongly than carbon due to its higher atomic number, appearing as the brightest feature in the image. Cross-correlation therefore maximally aligns the dopant positions between images, leading to the conclusion that the dopant never moves, "which is known to be false." The method overfits to the most salient image feature rather than aligning the lattice as a whole.

  • Iterative Closest Points (ICP) on extracted atom positions: ICP treats the detected atom positions as two point clouds and finds the rigid transformation that minimizes the distance between them, weighting all atoms equally (dopant and carbon). This avoids the dopant-dominance problem but is "quite sensitive to failures in atom detection" β€” if atom detection misses a few atoms or incorrectly identifies a noise artifact as an atom, the alignment can be thrown off.

The learned alignment approach. The paper instead trains a denoising convolutional neural network (following Jain and Seung, 2008) that predicts drift directly from image stacks. The network takes as input a sequence of image observations (o_1, ..., o_n) and outputs a predicted two-dimensional shift vector dΜ‚_n representing the drift between o_{n-1} and o_n. The historical observations o_1, ..., o_{n-2} provide context and noise reduction but are not used in the loss β€” they serve to help the network distinguish actual lattice structure from noise.

After prediction, the alignment is applied procedurally: the current observation o_n is shifted by -dΜ‚_n to bring it into register with o_{n-1}, and the aligned observation is appended to the history for the next step.

Training data: synthetic drift on idealized lattices. Since ground-truth drift values are not available for real microscope data (you cannot measure the true drift independently), the network is trained entirely on synthetic data. The training set consists of synthetic trajectories, each containing sequential image observations of a doped graphene system under random, correlated drift. The drift is modeled as a temporally correlated random variable β€” it does not jump arbitrarily between frames but evolves smoothly, as real specimen drift does.

To promote robustness, the paper applies substantial data augmentation at the trajectory level:

  • Random atom dropout: Some atoms are randomly removed from the synthetic images.
  • Bright contamination: Regions of bright contamination are introduced (mimicking beam-induced artifacts).
  • Synthetic holes: Large holes are added to the system (simulating lattice defects).

These augmentations ensure the network learns to align based on the overall lattice pattern rather than relying on any single feature that might be absent in real data.

Architecture and training. The network is parameterized as "six convolutional layers followed by downsampling, followed by a single fully-connected layer." The paper does not specify kernel sizes, channel counts, or activation functions. Training uses mean squared error loss between the predicted drift dΜ‚_n and the known synthetic drift d_n. The fully-convolutional-then-FC architecture is standard for image-to-scalar regression tasks.

Iterative refinement β€” a critical performance multiplier. Because drift prediction is a denoising task (the true drift is partially obscured by image noise and atom detection uncertainty), the network can be applied iteratively for progressively more precise correction. After shifting the image by the initial prediction dΜ‚_n, the network can be re-applied to the shifted pair to estimate any residual drift, and so on. The paper states that this iterative application "has a very large impact on performance."

The bottom-right panel of Figure 3 shows qualitative evidence: a sequence of three alignment iterations where the discrepancy between estimated atom positions in consecutive scans (orange dots for previous scan, blue dots for current scan, with red dots marking dopants) visibly shrinks with each iteration. Quantitatively, the paper reports that a transition model trained on data aligned with only a single pass "produces markedly different estimates of the optimal beam position, which are not able to successfully cause transitions when applied to the greedy controller" β€” a direct downstream consequence of alignment quality. This comparison is referenced as "Past Neighbor" in Figure 4, representing a controller using a model trained on insufficiently aligned data.

Data Filtering, Augmentation, and Standardization

The raw aligned images contain atom detection outputs β€” estimated positions of carbon and silicon atoms in the before and after states β€” but not every trial is usable for training. The filtering pipeline enforces strict criteria to ensure each training example represents a clean, interpretable transition event on a pristine lattice.

Filtering criteria (Section 4.3). Starting from 6,754 examples, the following filters are applied in sequence (the paper lists them but does not specify whether the order matters):

  1. Missing beam position: Examples where no beam position was recorded are discarded. This removes 793 examples (β‰ˆ12% of total). A missing beam position makes the example useless for learning the beamβ†’outcome mapping, since the input is absent.

  2. Dopant count β‰  1: Examples where the detected number of dopant atoms is not exactly one before the transition, or not exactly one after the transition, are discarded. This removes only 4 more examples (now at 797 discarded). A count other than one could indicate an atom detection error, a dopant that left the field of view entirely, or the presence of additional contamination that would violate the single-dopant assumption.

  3. Neighbor count β‰  3: Examples where the dopant does not have exactly three carbon neighbors before and after the transition are discarded. This is the largest filter, removing 3,593 additional examples. The paper attributes this to "either because they are absent, indicating non-pristine graphene, or were not detected." In non-pristine graphene, missing carbon atoms create vacancies, altering the local bonding environment and making the transition dynamics different from the nominal single-dopant case. Detection failures can also cause a valid 3-neighbor configuration to appear as having 2 or 4 neighbors.

  4. Neighbor position consistency: For the remaining examples, the paper checks that "the neighbors after the transition approximately aligned with the neighbors before the transition." This is quantified as an average distance > 0.71 Γ… between corresponding neighbor pairs. This filter removes 411 more examples. The purpose is to catch cases where the alignment procedure failed or the lattice was locally distorted by beam damage, resulting in neighbor positions that cannot be reconciled with the idealized hexagonal lattice geometry.

Total survival rate: After all filters, 1,953 examples remain β€” approximately 28.9% of the original 6,754. The paper treats this 80% discard rate matter-of-factly, but it has significant implications: the effective data efficiency of the microscope is low, meaning many hours of instrument time are spent collecting examples that ultimately cannot be used. This is presented as a consequence of the messy reality of STEM data rather than a flaw in the method, but it underscores the importance of the filtering pipeline β€” without it, the training data would contain a large fraction of corrupted or ambiguous examples that would degrade the learned model.

Coordinate standardization (frame-of-reference transformation). Once valid examples are identified, they are transformed into a consistent coordinate system to eliminate irrelevant variation:

  1. Translation to dopant-centric coordinates: The beam position is expressed relative to the current position of the dopant, with the dopant placed at the origin (0, 0). This removes any dependence on absolute position in the image.

  2. Rotation to canonical orientation: The carbon neighbor closest to the beam position is labeled as "neighbor 1." The entire system (beam position, neighbor positions) is then rotated so that this atom lies on the positive x-axis.

  3. Counter-clockwise labeling: The remaining two neighbors are numbered 2 and 3 in counter-clockwise order, completing the classification targets.

  4. "No movement" label: The outcome where the dopant remains in place is assigned index 0, making this a 4-way classification problem: classes {0, 1, 2, 3} where 0 = no transition, and {1, 2, 3} correspond to transitions to the three carbon neighbors.

This standardization is illustrated in the top-center panel of Figure 1, where the numbered neighbors are shown relative to the dopant center.

Why this particular labeling scheme? The paper notes that "there is no systematic difference between the three neighboring atoms; only their distance from the beam separates them." In an ideal hexagonal lattice with a single substitutional dopant, the three carbon neighbors are crystallographically equivalent β€” any apparent difference between them in a given trial is an artifact of the beam position and the coordinate system. The labeling scheme makes neighbor identity depend purely on beam position, which is what the model needs to learn. Rotating the system so neighbor 1 is always on the x-axis removes the continuous rotational degree of freedom, turning a regression problem over continuous angles into a classification problem over three discrete labels.

Data augmentation for rotation and reflection invariance. After standardization, the paper applies data augmentation that explicitly enforces the physical symmetries of the system:

  1. Reflection across the x-axis with 50% probability: This exchanges the labels for neighbors 2 and 3 (since neighbor 1 remains on the x-axis). Applying this randomly means the model sees both (beam-left-of-axis β†’ neighbor 2) and (beam-right-of-axis β†’ neighbor 2) as equivalent patterns, learning that neighbors 2 and 3 are indistinguishable aside from their angular position relative to the beam.

  2. Rotation by 0Β°, 120Β°, or 240Β° with equal probability: The three neighbors are arranged at 120Β° intervals around the dopant. Rotating the system by multiples of 120Β° permutes the neighbor indices (1 β†’ 2 β†’ 3 β†’ 1) while preserving the lattice geometry. Applying all three rotations equally means the model sees each configuration in all three possible cyclic permutations.

  3. Effective sixfold increase: The combination of optional reflection (Γ—2) and ternary rotation (Γ—3) yields 2 Γ— 3 = 6 equally probable augmentations per raw example. The top-right panel of Figure 3 shows the beam positions post-augmentation β€” the spatial coverage is visibly denser and more symmetric than in the raw data (center panel).

Why this augmentation is necessary (and why it works): The physical system is invariant under these transformations β€” rotating the entire graphene sheet or looking at it in a mirror does not change the physics of beam-induced transitions. The raw data, however, is collected in a fixed laboratory coordinate system and therefore has an arbitrary orientation. Without augmentation, the model would need to learn rotation invariance from the data, requiring a much larger dataset. Augmentation injects this invariance as an inductive bias, effectively telling the model "whatever you learn at one orientation applies equally to all orientations 120Β° apart, and to the mirror image." This is valid precisely because the 3-fold coordinated graphene lattice has hexagonal symmetry.

Learning the Transition Dynamics

Problem formulation. The goal is to estimate:

P(Sβ€²βˆ£s0,a)P(S' \mid s_0, a)

where $S'$ is the position of the silicon dopant at the next time step, $s_0$ is its current position, and $a$ is the beam action specified by a two-dimensional coordinate $x$ (beam placement relative to the dopant) and a duration $\Delta t$ in seconds (dwell time). The output space consists of four possibilities: no movement (stay at $s_0$), or hop to one of the three neighboring carbon sites (labeled 1, 2, 3).

Why decompose into total rate and neighbor distribution? The paper imposes a structural decomposition motivated by the physical constraint that "the probability of moving to another state should be monotonically increasing in $\Delta t$." A naive classification output (a 4-way softmax over the four possible outcomes) would not naturally encode this monotonicity β€” the model could, in principle, predict a decreasing probability of transition as dwell time increases, which is physically impossible (longer exposure to the electron beam cannot make a transition less likely).

The solution is to decompose the prediction into two components with a parametric form that guarantees monotonicity:

  1. Total transition rate $\lambda$: A scalar representing the instantaneous hazard rate of any transition occurring. The probability that some transition occurs within dwell time $\Delta t$ is modeled as an exponential cumulative distribution function:

P(Sβ€²β‰ s0∣s0,a)=1βˆ’eβˆ’Ξ»Ξ”tP(S' \neq s_0 \mid s_0, a) = 1 - e^{-\lambda \Delta t}

where $\lambda = \lambda(x, \Delta t)$ is a function of the beam position $x$ (and possibly dwell time itself, though the paper does not specify whether $\lambda$ depends on $\Delta t$ beyond its role in the exponential). $e$ is the base of the natural logarithm.

What it computes: the probability that at least one hop occurs during a dwell of length $\Delta t$, given the rate $\lambda$. When $\Delta t = 0$, the probability is zero (no chance of a transition with zero exposure); as $\Delta t \to \infty$, the probability approaches 1 (given enough time, a transition eventually occurs). For intermediate dwell times, the probability increases monotonically and smoothly.

Why this form: the exponential CDF is the standard survival model for events that occur at a constant hazard rate (memoryless property β€” the probability of a transition in the next infinitesimal interval depends only on the current state, not on how long the beam has already been applied). This is the simplest parametric form that enforces monotonicity in $\Delta t$. The paper cites Voter (2007), a reference on kinetic Monte Carlo methods, which commonly use exponential transition rates. The key property is that $1 - e^{-\lambda \Delta t}$ is guaranteed to be between 0 and 1 and guaranteed to increase with $\Delta t$ for any positive $\lambda$ β€” the model cannot violate physical plausibility regardless of what $\lambda$ value it predicts.

If per-neighbor rates are desired, they are obtained by multiplying the total rate by the categorical probabilities: $\lambda_y = \lambda \cdot y_k$ for neighbor $k$.

  1. Categorical distribution over next states $y$: If a transition occurs, which neighbor does the dopant move to? This is a 3-way categorical distribution $y = (y_1, y_2, y_3)$ with $\sum_k y_k = 1$, representing $P(S' = \text{neighbor } k \mid s_0, a, S' \neq s_0)$ β€” the probability of moving to each neighbor, conditioned on the fact that a transition occurs at all.

This decomposition means the full transition probability for neighbor $k$ is:

P(Sβ€²=neighborΒ k∣s0,a)=(1βˆ’eβˆ’Ξ»Ξ”t)β‹…ykP(S' = \text{neighbor } k \mid s_0, a) = (1 - e^{-\lambda \Delta t}) \cdot y_k

The probability of no movement is $e^{-\lambda \Delta t}$.

Loss functions. The model is trained with maximum likelihood estimation using two loss terms that are summed (Equation 3: $J_{\text{total}} = J_{\text{rate}} + J_{\text{next}}$).

The rate loss (Equation 1) penalizes the model's predicted total transition rate based on whether any transition actually occurred:

Jrate=βˆ’I(Sβ€²β‰ s0)β‹…(βˆ’Ξ»Ξ”t)βˆ’I(Sβ€²=s0)log⁑(1βˆ’exp⁑(βˆ’Ξ»Ξ”t))J_{\text{rate}} = -\mathbb{I}(S' \neq s_0) \cdot (-\lambda \Delta t) - \mathbb{I}(S' = s_0) \log(1 - \exp(-\lambda \Delta t))

where $\mathbb{I}(\cdot)$ is the indicator function, equal to 1 when its argument is true and 0 otherwise, $S'$ is the observed next position, $s_0$ is the current position, $\lambda$ is the predicted total rate, and $\Delta t$ is the dwell time.

What it computes: the negative log-likelihood of the observed binary outcome (transition occurred or did not occur) under the exponential CDF model. When a transition occurs $(\mathbb{I}(S' \neq s_0) = 1)$, the first term is active and reduces to $\lambda \Delta t$ (penalizing small $\lambda$ when a transition happened β€” the model should have predicted a high rate). When no transition occurs $(\mathbb{I}(S' = s_0) = 1)$, the second term is active: $-\log(1 - e^{-\lambda \Delta t})$, which penalizes large $\lambda$ when no transition happened (the model should have predicted a low rate). The sum is a scalar representing how well the rate parameter explains the observed binary outcome.

Why this form: this is the standard negative log-likelihood for a binary outcome under an exponential survival model. Minimizing it finds the $\lambda$ value that makes the observed pattern of transitions and non-transitions most probable. Alternative forms (like mean squared error between predicted and observed transition frequency) would not properly account for the varying dwell times β€” a non-transition at $\Delta t = 10$ seconds is stronger evidence for a low rate than a non-transition at $\Delta t = 1$ second, and the likelihood formulation handles this automatically through the exponential term.

The next-state loss (Equation 2) penalizes the model's predicted neighbor distribution only on trials where a transition occurred:

Jnext=βˆ’I(Sβ€²β‰ s0)(Sβ€²β‹…log⁑y)J_{\text{next}} = -\mathbb{I}(S' \neq s_0)(S' \cdot \log y)

where $S'$ is a one-hot vector encoding which neighbor the dopant moved to (or the zero vector if no move), $y$ is the predicted categorical distribution over the three neighbors, $\log y$ is the element-wise logarithm, and $S' \cdot \log y$ computes the log-probability assigned to the actually-chosen neighbor.

What it computes: the standard categorical cross-entropy between the observed neighbor choice and the predicted distribution, but only on examples where a transition actually occurred (the indicator function zeros out the loss when no movement happened, since there is no neighbor to predict). If the dopant moved to neighbor 2, the loss is $-\log y_2$, which heavily penalizes the model if $y_2$ is very small.

Why this form: this is the maximum-likelihood objective for a categorical variable, and restricting it to only transition examples makes sense because the "which neighbor" question is undefined when no transition occurred. The total loss $J_{\text{total}}$ can be interpreted as the joint negative log-likelihood of observing both the binary outcome and (conditional on a transition) the specific neighbor, under the assumption that these two aspects are independent given the model parameters.

Network architecture and training hyperparameters. The paper uses a "three-layer neural network" with ReLU hidden layer nonlinearities. The exact layer widths are not specified, but the small size (three layers) reflects the modest dimensionality of the input (beam position $x$ as a 2D coordinate, plus dwell time $\Delta t$ β€” at most 3 input features, depending on whether $\Delta t$ is provided as a separate input or absorbed into the rate computation).

Training uses:

  • Optimizer: Adam with weight decay (Kingma and Ba, 2015). No specific learning rate or weight decay value is given.
  • Loss: the summed $J_{\text{total}}$ from Equation 3, computed as cross-entropy.
  • Epochs: 500.
  • Batch size: 256.
  • Output activations: $\lambda$ (total rate) uses softplus activation (a smooth approximation to ReLU that guarantees positive outputs: $\text{softplus}(x) = \log(1 + e^x)$), which is necessary because $\lambda$ must be non-negative for the exponential CDF to be valid. $y$ (neighbor distribution) uses softmax activation to produce a valid probability distribution (non-negative, sums to 1).
  • Input normalization: all inputs are normalized to zero mean and unit variance prior to training, for stability. This is standard practice for neural networks with unbounded activation functions like ReLU.

Ensemble training and distillation. The paper trains multiple models on bootstrap-resampled versions of the training set (sampling with replacement to create different subsets). This ensemble approach serves two purposes:

  1. Uncertainty estimation: By examining the variance of predictions across ensemble members at a given beam position, the model can identify regions of input space where predictions are unreliable (high variance indicates insufficient data or conflicting signals). The paper does not explicitly use this uncertainty for control, but it is noted as a capability.

  2. Improved accuracy and robustness: The paper states that ensembling "significantly improved our overall accuracy and robustness." This is evaluated quantitatively in the synthetic experiments (Figure 8, left panel), where the distilled ensemble achieves lower regret than a single model across all data scales. Qualitatively, Figure 8 (right panel) shows that the rate function learned by the non-distilled model has irregular, jagged contours, while the distilled ensemble produces smoother, more physically plausible contours.

For deployment, the ensemble is distilled into a single transition predictor: the distilled model is trained (using "widely-sampled random beam positions and a large number of training steps") to match the ensemble's averaged predictions. This preserves the ensemble's accuracy while enabling faster inference (a single forward pass instead of multiple), which is important for real-time control where the model must be queried repeatedly as the dopant moves.

Result: on-neighbor is optimal. The learned model's prediction β€” extracted by finding the beam position $x$ that maximizes $P(S' = \text{neighbor } k \mid s_0, a)$ for each neighbor β€” converges to a clear spatial pattern: the optimal beam placement for inducing a transition to a given neighbor is directly on that neighbor. The paper reports a "50.0% (95% CI 0.246 to 0.754) probability of causing a transition with a five second dwell time, using a nominal beam current of 90 pA."

The center panel of Figure 1 visualizes this result as a contour map: three overlapping probability distributions (one per neighbor) are shown as colored contours on the graphene lattice. The contours for each neighbor peak at the neighbor's position and decay with distance, with the color coding (seen in the paper's figures) distinguishing which neighbor each set of contours corresponds to.

Synthetic Evaluation Framework

Because the real data has no ground-truth transition probabilities (only observed outcomes), the paper develops a synthetic evaluation framework to quantitatively assess the learning algorithm's behavior β€” its data scaling, its convergence properties, and its sensitivity to hyperparameter choices.

Generating synthetic rate functions. The paper samples synthetic transition probability distributions as mixtures of Gaussians, chosen because "they generalize the family of rate functions we expect to see in the real world by permitting multimodality, with the Gaussian nature of the distributions being sensible as the electron beam is approximately a Gaussian beam." Each synthetic rate function specifies the non-normalized transition rates $\lambda_y$ to neighboring states as a function of the beam position $x$. Figure 6 (right panel) shows representative examples β€” the contours for each neighbor form approximately Gaussian blobs centered somewhere in the vicinity of the neighbor position, with varying widths and amplitudes.

Standardizing maximum rate for fair comparison. To prevent comparisons between datasets from being confounded by different overall transition probabilities, the paper enforces "that the synthetic rate functions for each dataset have the same maximum value." This prevents extreme cases where one dataset consists of "entirely positive transitions or almost entirely negative transitions," which would make data scaling comparisons uninformative.

Dataset generation procedure. For each synthetic rate function, the paper:

  1. Generates a simulated graphene sheet with a single dopant.
  2. Uniformly samples random beam positions within 2 Γ… of the dopant.
  3. Simulates transitions according to the synthetic rate function (presumably by drawing from the exponential CDF for whether a transition occurs, and then from the categorical distribution for which neighbor).
  4. Continues sampling until a target number of positive transitions have been observed β€” because "positive transitions are generally far rarer than negative transitions, they are the critical determiner of effective dataset size."

Evaluation metric: mean squared error on a grid. After training a model on a synthetic dataset, the learned rate function $\hat{\lambda}_y(x)$ is compared to the ground-truth synthetic rate function $\lambda^{\text{true}}_y(x)$ across a uniformly-spaced 2D grid covering the region around the dopant. The mean squared error (MSE) aggregates the squared differences across all grid points and all neighbor channels. This provides a measure of how well the model has recovered the full rate function, not just the optimal beam position.

Control-relevant metric: maximum regret. While MSE measures average prediction accuracy, the paper argues that for control purposes, what matters is whether the model identifies the correct optimal beam position. Maximum regret is defined as (Equation 4):

Regret(R^)β‰œmax⁑aR(a)βˆ’R(arg⁑max⁑aR^(a))\text{Regret}(\hat{R}) \triangleq \max_a R(a) - R\left(\arg\max_a \hat{R}(a)\right)

where $R(a)$ is the true transition rate at beam position $a$ (i.e., the probability of causing any transition), $\hat{R}(a)$ is the learned model's predicted rate, $\arg\max_a \hat{R}(a)$ is the beam position the learned model believes is optimal, and $R(\arg\max_a \hat{R}(a))$ is the true rate at that believed-optimal position.

What it computes: the gap between the maximum possible transition rate (achievable if you knew the true rate function perfectly) and the rate you actually get by following the learned model's recommendation. A regret of 0 means the model correctly identifies the true optimal beam position; a regret of 0.3 means the model's chosen position achieves a transition rate 0.3 lower than the maximum possible (e.g., 0.4 vs. 0.7).

Why this form: MSE and regret measure fundamentally different things. A model can have low MSE (it captures the overall shape of the rate function well) but high regret (the argmax is slightly shifted from the true peak). Conversely, a model can have high MSE (it is wrong in regions far from the optimum) but zero regret (it correctly identifies the peak). For control, regret is the more relevant metric because the controller always chooses the believed-optimal action β€” it does not care about prediction accuracy in regions it never visits. Figure 7 (right panel) confirms this distinction: the model's MSE converges faster than its regret, meaning the overall shape of the rate function is learned before the precise location of the maximum is pinned down. The paper states this "matches our empirical experience where the learned rate functions can look similar although their argmax can differ (e.g., Learned Rates (Less Data) vs Learned Rates in Figure 4)."

Data scaling results (Figure 6, left panel). When models are trained on synthetic datasets of increasing size (measured by number of positive transitions, ranging from roughly 1 to 1,000), the MSE drops sharply once a few hundred positive transitions are available. With fewer than ~100 positive transitions, performance is poor and highly variable (wide confidence intervals across 30 synthetic datasets); above ~200–300, the model converges to low-error estimates. The paper states this "rapidly improves once hundreds of positive transitions are available, matching our own experience of the model's improvement as additional data was collected."

Model comparison results (Figure 7, left panel). The paper compares its neural rate model against two classical machine learning alternatives:

  • K-nearest neighbors: presumably using raw beam positions and dwell times as features and observed transitions as labels.
  • Random forest: an ensemble of decision trees.

Both alternatives are "also capable of learning reasonable transition models" but "generally require significantly more data to do so and ultimately converge to worse solutions." The neural network achieves lower regret at all data scales, with the gap being largest in the low-data regime. The paper attributes this to "inductive biases provided by modern neural networks" β€” the continuous, smooth function class that neural networks naturally represent is well-matched to the smooth, Gaussian-like spatial structure of true transition rate functions.

Ensemble distillation results (Figure 8, left panel). On synthetic data, the distilled ensemble achieves lower regret than a single non-distilled model at all data scales. The improvement is "largest in the intermediate-data regime when meaningful transition models can be learned but inaccuracies are common, matching our experience in the progression of real data experiments." The right panel of Figure 8 shows a qualitative comparison on real data: the non-distilled model's rate contours are irregular and jagged, while the distilled model's contours are smoother and more circular, suggesting the ensemble averaging removes spurious variations from individual models that overfit to noise in their bootstrap samples.

Control Strategies Evaluated

The greedy control algorithm. The controller uses the learned transition model to implement a simple greedy strategy:

  1. Compute the shortest path on the hexagonal lattice from the current dopant position to the goal position.
  2. Identify the first neighbor along this path.
  3. Query the learned model to find the beam position that maximizes the probability of transitioning to that specific neighbor.
  4. Apply the beam at that position with a fixed 5-second dwell time.
  5. Image to determine the outcome.
  6. Repeat until the goal is reached or a maximum number of attempts is exceeded.

This greedy strategy assumes that inducing one-hop transitions along the shortest path is optimal, which is reasonable given the hexagonal lattice structure but does not account for possible multi-hop jumps or alternative paths that might be faster.

Five beam-placement strategies compared (Figure 4). The paper evaluates five different strategies for beam placement, all using the same 5-second dwell time and 90 pA beam current:

  1. On neighbor: The proposed optimal strategy from the learned model. Place the beam directly centered on the neighboring carbon atom the dopant should move to.

  2. Short of neighbor: Place the beam between the dopant and the target neighbor β€” essentially the midpoint of the Si-C bond. This tests whether the knock-on mechanism is mediated by the bond itself rather than the carbon atom's nucleus.

  3. Past neighbor: Place the beam beyond the neighbor atom, on the far side from the dopant. This tests whether the knock-on requires the beam to push the carbon atom toward the dopant (which would favor beam placement between them) or can work from any direction.

  4. Perpendicular offset: Offset the beam perpendicular to the Si-C bond axis. This tests whether the optimal beam placement is direction-specific or merely proximity-based.

  5. Learned dynamics (less data): The optimal beam position according to a model trained on approximately half of the collected data. The resulting "optimal" placement was "just past the neighbour" β€” i.e., past the neighbor atom but closer to it than the "Past Neighbor" condition. This serves as a validation that additional data meaningfully changed the model's prediction.

Experimental protocol. For each strategy, the controller attempts to move the dopant from a starting position to a randomly chosen goal position, using the strategy's beam placement at each step. The number of beam pulses required (attempts) and whether each pulse successfully induces the intended transition are recorded.

Results (Figure 4, left panel). The "On neighbor" strategy achieves approximately a 50% transition success rate β€” roughly double the success rate of any other strategy, all of which fall below 25%. The "Past Neighbor" strategy (derived from a model trained on less data) performs particularly poorly, demonstrating that the specific beam position matters and validating the iterative data collection and model refinement process.

Successful autonomous trajectory (Figure 5). The paper presents a concrete demonstration: a five-step trajectory where the automated controller drives the silicon dopant to a pre-specified goal position (red arrows in Figure 5a). The HAADF-STEM images show the silicon (bright atom due to higher atomic number) at each step, while the predicted images (Figure 5b) show the atom detection output with the silicon depicted as a larger orange circle. The beam positions are shown as green circles. Notable observations:

  • The first step caused a multi-site jump (the silicon moved farther than one lattice spacing), despite the controller targeting only the nearest neighbor. The paper explains this as likely due to the lack of "real-time detector feedback to indicate if the silicon transitioned earlier than the designated dwell time" β€” the beam continued firing for the full 5 seconds after the dopant had already moved, potentially causing additional transitions.
  • The remaining four steps were single atomic jumps, suggesting that with feedback, multi-hop events could be avoided or intentionally exploited.
  • The path summary (Figure 5c) shows the step-by-step progression of the silicon atom toward the goal.

Implications of the multi-hop observation. The paper notes that the multi-hop behavior "can be exploited for more efficient beam manipulation; i.e., one beam position can intentionally induce more than one atomic jump." This suggests that future controllers could learn to aim for specific multi-hop outcomes (e.g., placing the beam such that the dopant jumps two sites in one dwell period), potentially accelerating manipulation. However, this would require the transition model to predict multi-hop probabilities, which the current model does not do β€” it only models single-hop outcomes.

4. Key Insights and Innovations

Innovation 1: Reframing Atomic Manipulation from a Physical Modeling Problem to a Data-Driven Control Problem

The paper's most fundamental conceptual move is rejecting the premise that you need to understand the physics of beam-matter interactions to control them. The dominant paradigm in the microscopy community β€” and indeed in much of materials science β€” treats atomic manipulation as a problem of mechanistic understanding: if you can model the knock-on processes, ionization effects, sputtering mechanisms, and phonon-assisted transitions from first principles, you can then compute the optimal beam position. The paper's introduction explicitly documents this approach: "A number of theories for beam manipulation have been proposed, including those based on phonon-assisted knock-on and electronic excitations." The implicit assumption is that better physical models yield better control.

This paper inverts that logic entirely. Rather than building a physical model and deriving optimal actions from it, the paper treats the STEM as a black-box transition system and learns the mapping from actions (beam position, dwell time) to outcomes (dopant hop or no hop) directly from empirical data. The transition dynamics are not derived from physics; they are measured statistically. This is a genuinely different intellectual framing β€” it shifts the problem from "can we model the physics?" to "can we collect enough systematic data to characterize the probability surface?" β€” and it matters because the physics is genuinely complex (multiple interacting mechanisms, quantum-level effects, thermal noise) while the empirical surface is, as it turns out, relatively smooth and learnable.

The significance of this reframing extends beyond the specific Si-on-graphene system. It suggests a general methodology for automated atomic fabrication: for any dopant-substrate combination, run a systematic data collection campaign, learn the transition function, and deploy a controller β€” without ever needing to understand why the transitions occur the way they do. This is a fundamentally different path to automation than the physics-based modeling approach, and it sidesteps the bottleneck that has slowed progress in atomic manipulation: the difficulty of building accurate first-principles models for complex beam-induced dynamics.

The evidence that this reframing works is the 50% success rate of the learned "on neighbor" policy (Section 5, Figure 4), which required no physical modeling whatsoever β€” only data collection, alignment, filtering, and neural network training. The fact that this purely empirical approach confirms (rather than discovers) the heuristic that the community already believed is beside the point; the innovation is the methodology itself, which generalizes to configurations where no heuristic exists (as the paper explicitly notes: "For any other configuration, the rules are already not the same, and the optimal beam position for causing a transition event is not clear").

Innovation 2: The Pipeline as the Contribution β€” Establishing That Data Curation, Not Model Architecture, Is the Bottleneck in Scientific ML for Microscopy

The paper's architecture β€” a three-layer neural network with standard ReLU activations, trained with Adam and weight decay β€” is unremarkable from a machine learning perspective. This is not a weakness; it is precisely the point. The paper's genuine intellectual contribution is the demonstration that for this class of scientific machine learning problems, the hard work is not in model design but in data engineering: alignment, filtering, standardization, and augmentation constitute the intellectually novel components, while the learning algorithm itself is largely off-the-shelf.

This is a diagnostic insight with broad implications. The paper systematically works through each stage of the data pipeline and shows, with concrete evidence, why each step matters:

  • Alignment (Section 4.2): The paper shows that classical alignment methods fail β€” cross-correlation overfits to the bright dopant and concludes it never moves, while ICP is sensitive to atom detection failures. The learned CNN aligner, applied iteratively, is not just an incremental improvement; it is the enabling technique without which the entire downstream pipeline would produce garbage. The quantitative evidence is stark: a model trained on single-pass-aligned data produces controllers that cannot successfully cause transitions (the "Past Neighbor" result in Figure 4). This is not a small performance difference; it is the difference between a working system and a non-working one.

  • Filtering (Section 4.3): Approximately 80% of the collected data is discarded. This is not presented as a failure of data collection but as a necessary quality-control step that separates signal from noise. The paper's explicit documentation of what fraction of data fails each filter (missing beam position: 12%, neighbor count violations: 53%, etc.) provides a diagnostic breakdown that future practitioners can use to anticipate data yield and target collection improvements. This level of transparency about data quality is rare in ML papers and highly valuable for anyone attempting to replicate the approach.

  • Augmentation (Section 4.3): The rotation and reflection augmentation is not just a standard ML trick; it encodes the physical symmetries of the hexagonal lattice as an inductive bias, effectively multiplying the dataset size by 6Γ— at zero additional experimental cost. The paper's explicit justification β€” that the three carbon neighbors are crystallographically equivalent and that the system must be invariant under 120Β° rotations and reflections β€” demonstrates a principled approach to incorporating domain knowledge into data preparation rather than model architecture.

  • Parametric decomposition (Section 4.4): The factorization of transition probability into total rate (exponential CDF) and neighbor distribution (softmax) embeds the physical constraint that transition probability must be monotonically increasing in dwell time. This is not a model architecture innovation per se (exponential survival models and softmax classification are standard), but it is a loss-function-level encoding of physical knowledge that prevents the model from learning physically impossible predictions.

The synthetic experiments (Section 6) reinforce this pipeline-centric message. The comparison against KNN and random forests (Figure 7, left) shows that the neural network outperforms classical methods, but the real story is in Figure 8: ensemble distillation significantly improves robustness in the intermediate-data regime, and the qualitative difference between distilled and non-distilled rate functions on real data (Figure 8, right) shows that even with the same architecture, how you train and combine models matters enormously. The paper is, in effect, a case study in the principle that for real-world scientific data, the ML algorithm is the least important component; the data pipeline is everything.

This is a fundamental (not incremental) insight because it inverts the typical ML research priority β€” novel architectures β€” and redirects attention to the unglamorous but critical work of data engineering. For the microscopy community specifically, it provides a template for building automated control systems: invest in systematic data collection, build a careful alignment and filtering pipeline, enforce physical symmetries through augmentation, and only then apply standard learning algorithms. The specific neural network could be replaced with a random forest or a Gaussian process without changing the core contribution.

Innovation 3: Regret as a Control-Relevant Evaluation Metric That Reveals a Qualitative Gap Between Prediction Accuracy and Decision Quality

The paper introduces a distinction that is well-known in reinforcement learning and control theory but rarely applied in microscopy automation: the difference between predicting the rate function well on average (MSE) and identifying the optimal action (regret). This is formalized in Equation 4 and empirically demonstrated in Figure 7 (right panel):

Regret(R^)β‰œmax⁑aR(a)βˆ’R(arg⁑max⁑aR^(a))\text{Regret}(\hat{R}) \triangleq \max_a R(a) - R(\arg\max_a \hat{R}(a))

The conceptual innovation is not the equation β€” regret is a standard concept in decision theory and bandit algorithms. Rather, the innovation is recognizing that for this application, regret is the right metric and that it converges differently from MSE. Figure 7 (right) shows that MSE converges faster than regret as a function of dataset size. In practical terms: with a moderate amount of data, the learned rate function looks globally correct (low MSE), but the precise location of the maximum is still uncertain (high regret). This means looking at the contour plots (as in Figure 1, center panel) can be misleading β€” a model can produce visually plausible rate functions whose argmax is far from the true optimum.

This has direct consequences for the paper's own experimental narrative. The "Learned Rates (Less Data)" controller in Figure 4 was derived from a model trained on approximately half the collected data. That model's rate function presumably looked similar to the final model's β€” both likely showed the probability mass concentrated near the neighbor positions β€” but its argmax was shifted to "just past the neighbour" rather than directly on the neighbor. The resulting controller performed dramatically worse (below 25% success rate vs. ~50%). This is a vivid demonstration that visual similarity of learned functions does not imply control equivalence, and that data requirements for control are strictly higher than data requirements for qualitative modeling.

The broader significance of this insight is that it provides a principled way to determine when you have enough data. A practitioner could track both MSE and regret on held-out synthetic data (or on real data using leave-one-out cross-validation of controller performance) and stop collecting data when regret plateaus, rather than when MSE plateaus (which happens earlier). This is a concrete methodological recommendation that emerges from the conceptual distinction and is not obvious a priori β€” one might reasonably assume that a model that accurately predicts transition probabilities everywhere would also correctly identify the optimal action, but Figure 7 (right) shows this assumption can be false.

This is an incremental conceptual contribution (the regret concept itself is not new) but a fundamental practical insight for the specific domain. It changes how one should think about model evaluation for control tasks: the downstream task performance, not the intermediate prediction accuracy, is what matters, and the two can diverge qualitatively.

Innovation 4: The Negative Result That Data Requirements Are Substantial and Tightly Coupled to Positive-Transition Frequency

The paper contains an implicit but important negative finding: learning a usable transition model requires hundreds of positive transitions, and positive transitions are rare relative to total experimental trials. This is documented quantitatively through the synthetic scaling experiments (Figure 6, left panel) β€” performance is poor and highly variable below ~100 positive transitions and only stabilizes once several hundred are available β€” and qualitatively through the real-data experience, where the model trained on ~1,000 positive transitions (the "Learned Rates (Less Data)" condition) produced a controller that failed to generalize.

This matters because it establishes a concrete data budget for similar efforts. The initial dataset of 6,754 examples yielded only 1,953 valid examples after filtering (~29%), of which some fraction were positive transitions (the paper does not report this fraction, but since beam positions were uniformly sampled within a 2.84 Γ… disk and positive transitions presumably occur mainly when the beam is near a carbon neighbor, the positive rate is likely in the 10–30% range). This means that several thousand experimental trials β€” representing hours of STEM time β€” are necessary to achieve reliable automated control for a single dopant-substrate system.

This is a sobering but practically valuable finding. It tells future researchers: do not expect to collect a few hundred examples and get a working controller. The data appetite of this approach is substantial, and the filtering losses (80% in this case) mean that raw experimental throughput must be 5Γ— higher than the desired clean-dataset size. The paper does not frame this as a limitation to be overcome but simply as a reality of the method β€” and documenting it honestly is a service to the field.

The coupling to positive-transition frequency (rather than total trials) is also significant because it means that data collection efficiency depends on the transition probability itself. If a dopant-substrate system has lower inherent transition rates (requiring longer dwell times or more careful beam positioning to induce hops), the data collection campaign becomes proportionally longer. This creates a challenging cold-start problem: before you have a model, you don't know where to place the beam to maximize transition probability, so your early data collection is inefficient (few positive transitions), which means it takes longer to build a model, which means you spend more time in the inefficient regime. The paper's solution β€” uniform random sampling within a fixed radius β€” is simple but potentially wasteful for systems with low overall transition probability. This tension between exploration (gathering diverse data) and exploitation (maximizing positive-transition yield for faster model improvement) is not explored in the paper but is a natural direction for future work that the paper's characterization of the problem makes visible.

This is a fundamental practical insight rather than a theoretical advance. It reframes the problem from "can we learn transition dynamics?" (answered affirmatively) to "how much data does it take, and what does that imply for experimental design?" (answered quantitatively through synthetic scaling curves and qualitatively through the real-data progression).

5. Experimental Analysis

Evaluation Methodology

  • Dataset. The real-world dataset consists of 6,754 raw experimental trials collected on a Nion UltraSTEM 100 microscope, each trial recording a beam position, dwell time, and before/after images of a single silicon dopant on a graphene lattice. After filtering (Section 4.3), 1,953 clean examples remain for training. The synthetic evaluation framework (Section 6) uses 30 independently generated datasets, each with at least 1,000 positive transitions, sampled from random mixture-of-Gaussian rate functions on a simulated hexagonal lattice with a single dopant.

  • Base model(s). The transition dynamics model is a three-layer neural network with ReLU hidden layer nonlinearities, trained using Adam with weight decay (Kingma and Ba, 2015). The architecture modestly reflects the low-dimensional input (beam position as a 2D coordinate, plus dwell time). The atomic alignment network (Section 4.2) is a separate convolutional neural network with six convolutional layers followed by downsampling and a single fully-connected layer, trained on synthetic drift data using mean squared error. Real-time atom detection during data collection uses deep ensemble neural networks from Ghosh et al. (2021).

  • Metrics. Two primary evaluation regimes are used, reflecting the absence of ground-truth transition probabilities. For the real-data controller validation (Section 5), the metric is transition success rate β€” the fraction of beam pulses that successfully induce the intended dopant transition to the target neighbor, measured across multiple attempts per strategy. For synthetic data (Section 6), mean squared error is computed between the learned rate function and the ground-truth synthetic rate function on a uniformly-spaced 2D grid around the dopant, and maximum regret (Equation 4) measures the gap between the true maximum transition rate and the true rate at the learned model's argmax. The paper also reports the 95% confidence interval for the on-neighbor transition probability (0.246 to 0.754 at 5-second dwell time, 90 pA beam current).

  • Baselines. Five beam-placement strategies are compared in the real-data controller experiments (Section 5, Figure 4):

    • On neighbor: The proposed optimal strategy from the learned model β€” beam placed directly on the target carbon neighbor.
    • Short of neighbor: Beam placed between the dopant and the target neighbor.
    • Past neighbor: Beam placed beyond the target neighbor atom.
    • Perpendicular offset: Beam offset perpendicularly from the Si-C bond axis.
    • Learned dynamics (less data): The optimal beam position according to a model trained on approximately half of the collected data, which produced a placement "just past the neighbour."

    In the synthetic experiments (Section 6, Figure 7 left), the neural rate model is compared against K-nearest neighbors and a random forest classifier as alternative learning algorithms. The ensemble-distilled model is compared against a non-distilled single model (Figure 8).

  • Generation budget / compute accounting. The "compute budget" in real experiments is measured in terms of the number of electron beam pulses (attempts to induce a transition), with each pulse using a constant 5-second dwell time at a nominal beam current of 90 pA (approximately 3 billion electrons per pulse). The controller operates until the dopant reaches the goal or a maximum number of attempts is exhausted. In synthetic experiments, dataset size is measured by the number of positive transitions observed, since these are the critical determiner of effective training data (negative transitions are far more common and provide less information per example).

  • Cross-validation / statistical protocol. For the real-data experiments, no cross-validation or statistical significance testing is reported for the controller comparisons β€” the results in Figure 4 are presented as raw transition success rates across the five strategies. For synthetic experiments (Section 6), 30 independently-generated synthetic rate functions are used, and results are reported with bootstrapped confidence intervals across these datasets at each data scale (Figure 6, left panel; Figure 7, left panel). The ensemble distillation comparison (Figure 8, left) is evaluated across a "suite of synthetic datasets." The 95% confidence interval for the on-neighbor transition probability (0.246 to 0.754) is reported but the method for computing it is not specified.

Main Quantitative Results

On-Neighbor Beam Placement as the Optimal Strategy

The primary real-world experimental result is that the learned model's optimal beam placement β€” directly on the target carbon neighbor β€” achieves a transition success rate approximately twice that of any alternative strategy. Specifically, Figure 4 (left panel) reports:

"the on neighbor strategy induces the intended transition on average approximately 50% of the time, whereas the other approaches are below 25%"

The paper reports this as "50.0% (95% CI 0.246 to 0.754) probability of causing a transition with a five second dwell time, using a nominal beam current of 90 pA." The wide confidence interval reflects the inherent stochasticity of beam-induced transitions and, presumably, the limited number of attempts per strategy, though the paper does not report the exact number of trials conducted for each strategy.

The four alternative strategies (Short of Neighbor, Past Neighbor, Perpendicular Offset, Learned Rates with Less Data) all achieve transition success rates below approximately 25%, with the "Past Neighbor" condition (representing a model trained on insufficient data) performing particularly poorly. The bar chart in Figure 4 (left) shows the magnitude of the gap visually, with "On Neighbor" reaching roughly 50% and the alternatives clustered in the 10–25% range.

This result quantitatively confirms what was previously "anecdotally held to be true by the microscopy community" β€” that the optimal beam placement is on the neighboring carbon atom β€” but provides the first explicit probability measurement and confidence interval, transforming the heuristic into a quantified parameter usable for automation.

Demonstration of Fully Automated Dopant Trajectory

Figure 5 provides qualitative evidence that the learned model enables closed-loop automated control: a five-step trajectory where the controller successfully drives the silicon dopant to a pre-specified goal position (marked by red arrows). The HAADF-STEM image snapshots (Figure 5a) show the silicon as the bright atom at each intermediate position, while the predicted atom detection outputs (Figure 5b) show the silicon as a larger orange circle and the beam positions as green circles. The path summary (Figure 5c) diagrams the step-by-step progression.

A notable observation from this trajectory: the first beam pulse caused a multi-site jump (the dopant moved farther than a single lattice spacing), while subsequent pulses resulted in single atomic hops. The paper attributes the initial multi-hop to the absence of real-time feedback β€” "Real-time detector feedback was not used to indicate if the silicon transitioned earlier than the designated dwell time, and therefore this was one limitation in the current work." This is presented not as a failure but as a feature that "can be exploited for more efficient beam manipulation; i.e., one beam position can intentionally induce more than one atomic jump."

The trajectory demonstrates the full pipeline in operation: real-time atom detection (using deep ensemble neural networks from Ghosh et al., 2021) feeds atomic coordinates to the controller, which selects beam positions according to the learned transition model, and the cycle repeats until the goal is reached. No human intervention is required between steps.

Synthetic Data Scaling: Convergence Requires Hundreds of Positive Transitions

Figure 6 (left panel) shows the scaling behavior of the neural rate model on synthetic data as a function of the number of positive transitions in the training set. The y-axis plots the sum of squared prediction error (MSE) on a log scale, while the x-axis plots the number of positive transitions on a log scale ranging from approximately 1 to 1,000. The results, averaged over 30 synthetic datasets with bootstrapped confidence intervals, show:

  • Below ~30 positive transitions: MSE is very high (on the order of 10³–10⁴) with wide confidence intervals, indicating that the model is essentially unable to learn anything useful from such sparse data.

  • Between ~30 and ~200 positive transitions: MSE drops sharply, crossing below 10Β² around 100 positive transitions. The confidence intervals narrow considerably in this regime, indicating that model performance becomes more reliable across different synthetic rate functions.

  • Above ~200–300 positive transitions: MSE stabilizes at values below 10ΒΉ, with narrow confidence intervals. The paper characterizes this as convergence: "our model has very poor performance with limited amounts of data, but rapidly improves once hundreds of positive transitions are available."

The paper explicitly connects this synthetic scaling behavior to the real-world data collection experience: "matching our own experience of the model's improvement as additional data was collected." This validation is important because the synthetic rate functions are mixtures of Gaussians β€” chosen to be broadly representative of expected physical rate functions β€” but the convergence behavior is consistent with the progression from the "Learned Rates (Less Data)" model (trained on ~1,000 real positive transitions, which produced an incorrect argmax) to the final model (trained on ~2,000 positive transitions, which converged to the correct on-neighbor optimum).

Regret Converges More Slowly Than MSE

Figure 7 (right panel) compares the rate of convergence of two evaluation metrics β€” mean squared error and maximum regret β€” as a function of the number of positive transitions in the training set. The y-axis shows "% Difference From Final Performance," normalized so that both metrics asymptotically approach 0 as dataset size grows. The key finding:

"the model tends to converge more quickly to the global shape of the rate function (as measured by the mean squared error) as compared to true argmax (as measured by the regret)"

In the regime of ~10–100 positive transitions, MSE has already dropped to within ~20–30% of its asymptotic value, while regret remains at ~40–60% of its initial value. This means that with moderate data, the learned rate function is globally accurate (low MSE) but the precise location of the maximum is still substantially wrong (high regret), directly explaining why the "Learned Rates (Less Data)" model produced rate functions that looked qualitatively similar to the final model (both showed probability mass near neighbor positions) but whose argmax was shifted to "just past the neighbour," resulting in dramatically worse control performance.

The paper states this divergence "matches our empirical experience where the learned rate functions can look similar although their argmax can differ (e.g., Learned Rates (Less Data) vs Learned Rates in Figure 4)." This is presented not as a theoretical result but as an empirical validation of the regret metric's practical relevance.

Neural Network Outperforms Classical ML Methods, Especially in the Low-Data Regime

Figure 7 (left panel) compares the neural rate model against K-nearest neighbors and a random forest classifier as a function of the number of positive transitions in the training set. The y-axis plots maximum regret (0 to 1 scale), with lower values indicating better identification of the true optimal beam position. All three methods improve with more data, but:

  • At all data scales, the neural rate model achieves lower regret than both KNN and random forest.
  • In the low-data regime (fewer than ~100 positive transitions), the gap is largest β€” the neural network maintains regret around 0.4–0.6 while both classical methods are at or above 0.8.
  • At convergence (1,000 positive transitions), the neural network achieves near-zero regret, while KNN and random forest converge to regret values around 0.1–0.2 β€” better than their low-data performance but still measurably worse than the neural network.

The paper attributes this advantage to "inductive biases provided by modern neural networks" β€” specifically, the continuous, smooth function class that neural networks naturally represent is well-matched to the Gaussian-like spatial structure of true transition rate functions, while distance-based methods (KNN) and axis-aligned decision boundaries (random forests) are less well-suited to modeling smooth spatial probability distributions.

Ensemble Distillation Improves Robustness, Especially with Intermediate Data

Figure 8 (left panel) compares the regret of a single (non-distilled) model against a distilled ensemble across the same range of dataset sizes. The distilled ensemble achieves lower regret at all data scales, with the improvement being:

"largest in the intermediate-data regime when meaningful transition models can be learned but inaccuracies are common"

In the regime of ~30–100 positive transitions, the distilled ensemble's regret is approximately 0.2–0.3 lower (on a 0–1 scale) than the non-distilled model β€” a substantial improvement in the region where models are learnable but unreliable. At very small datasets (~10 positive transitions), both methods perform poorly; at very large datasets (~1,000 positive transitions), both converge to near-zero regret, and the gap narrows.

Figure 8 (right panel) provides qualitative evidence on real data: the distilled model's rate contours (shown for one neighbor on a 4 Γ… Γ— 4 Γ… grid centered on the dopant) are smooth and approximately circular, while the non-distilled model's contours are irregular, jagged, and contain multiple disconnected islands. The paper presents this as visual evidence that ensembling removes spurious variations from individual models overfitting to noise in their bootstrap samples, resulting in more physically plausible (smooth, unimodal) rate functions.

Ablation Studies and Robustness Checks

Alignment quality: A transition model trained on data aligned with only a single pass of the convolutional aligner (versus iterative multi-pass alignment) produces markedly different estimates of the optimal beam position, and the resulting controller "is not able to successfully cause transitions when applied to the greedy controller." This is evidenced by the "Past Neighbor" strategy in Figure 4, which represents the optimal policy from a model trained on insufficiently-aligned data and achieves transition success rates below 25%. The bottom-right panel of Figure 3 shows qualitative evidence that alignment quality improves visibly with additional iterations. This ablation is critical because it demonstrates that alignment is not merely a preprocessing nicety but an enabling step without which the entire pipeline fails.

Alternative alignment methods: Cross-correlation alignment fails because "images of this system are generally dominated by the very bright silicon dopants," causing alignment to always center on the dopant and leading to the false conclusion that it never moves. Iterative Closest Points (ICP) on extracted atom positions is "quite sensitive to failures in atom detection." The learned CNN aligner was chosen specifically because it overcomes both limitations β€” it does not overfit to the dopant brightness (because it is trained on synthetic data with multiple atoms present) and is robust to detection failures (because it operates on raw or lightly-processed images rather than discrete atom coordinates).

Data filtering criteria: Starting from 6,754 raw examples, the sequential filters (missing beam position: 793 removed; dopant count β‰  1: 4 more removed; neighbor count β‰  3: 3,593 more removed; neighbor position inconsistency: 411 more removed) collectively discard approximately 80% of the initial data, leaving 1,953 examples. The paper does not report ablation experiments showing what happens if filtering is relaxed, but the synthetic scaling experiments (Figure 6) imply that including corrupted or ambiguous examples would degrade model performance, particularly in the critical low-to-intermediate data regime where every training example matters. The neighbor-count filter (removing 3,593 examples, or ~53% of raw data) is by far the largest, suggesting that non-pristine graphene configurations and atom detection failures are the dominant sources of data loss.

Data augmentation (rotation and reflection): The paper does not report an explicit ablation comparing performance with and without augmentation. However, the justification for augmentation is grounded in physical symmetry β€” the 3-fold coordinated graphene lattice is invariant under 120Β° rotations and reflections β€” and the effective 6Γ— increase in data coverage (Figure 3, top-right panel versus top-center panel) is substantial. Given the synthetic scaling curves (Figure 6) showing that performance is data-limited below several hundred positive transitions, a 6Γ— effective increase in dataset size would correspond to a meaningful shift along the x-axis of those curves, moving from the high-MSE, high-regret regime toward convergence. The paper's reliance on this augmentation is implicitly validated by the fact that the final model converges to physically sensible (on-neighbor) optimal beam positions despite having only ~2,000 real examples β€” without augmentation, the effective dataset size would be one-sixth as large.

Model architecture alternatives (KNN and Random Forest): As discussed in the quantitative results (Figure 7, left), both K-nearest neighbors and random forest classifiers are "capable of learning reasonable transition models" but converge to higher regret than the neural network and require more data to do so. This comparison serves as a robustness check that the neural network architecture is not spurious β€” alternative learning algorithms can extract signal from the data, but the neural network's inductive biases (smooth, continuous function approximation) are better matched to the problem structure.

Ensemble vs. single model: The distilled ensemble achieves lower regret than a non-distilled single model at all data scales in synthetic experiments (Figure 8, left), and produces qualitatively more regular rate functions on real data (Figure 8, right). The paper states this "significantly improved our overall accuracy and robustness." The distillation step (training a single model to match the ensemble's averaged predictions) serves a practical purpose β€” enabling faster inference for real-time control β€” without sacrificing the ensemble's improved generalization. This is not presented as an ablation per se, but the comparison against the non-distilled model in Figure 8 demonstrates that the ensemble approach provides non-trivial gains.

Dwell time consistency: All controller experiments (Section 5) use a constant 5-second dwell time at 90 pA beam current, removing dwell time as a variable for the real-data validation. The paper does not explore whether the learned model's predictions for different dwell times are accurate β€” the exponential CDF form enforces monotonicity (Section 4.4), but the synthetic evaluation framework (Section 6) does not include explicit dwell-time ablation experiments. The learned rate function is evaluated primarily through its spatial predictions (optimal beam position) at fixed dwell time, not through its temporal predictions (how probability varies with Ξ”t).

Beam current: All experiments use a nominal beam current of 90 pA. The paper notes that electron dose (beam current Γ— dwell time) is the physically relevant quantity, providing the conversion that 5 seconds at 90 pA corresponds to approximately 3 billion electrons. However, no experiments vary beam current independently of dwell time to verify that the exponential CDF model correctly captures the dose-dependence. The model treats Ξ”t as a continuous input but does not separately model beam current, which is held constant.

Critical Assessment

Does the paper demonstrate that the learned model enables automated atomic manipulation?

Yes, with the caveat that only one complete trajectory is shown. Figure 5 provides a single five-step trajectory demonstrating successful automated dopant movement to a goal position. This is a compelling existence proof but does not constitute a statistical characterization of controller reliability. The paper does not report:

  • How many trajectories were attempted.
  • The success rate of full trajectories (versus per-step transition success rate).
  • The distribution of trajectory lengths (number of steps to reach the goal).
  • Whether the controller ever fails to reach the goal or causes the dopant to move in unintended directions.

The per-step transition success rate of ~50% for the on-neighbor strategy (Figure 4) implies that a trajectory of N steps will succeed with probability approximately (0.5)^N if each step is independent. A five-step trajectory would have only about a 3% chance of completing without any failed pulses requiring retries, suggesting that the controller described in Section 5 must include retry logic (repeatedly attempting the same step until it succeeds) that is not explicitly characterized. The "maximum allowable attempts" mentioned in the protocol is not specified, so the controller's effective reliability cannot be assessed from the reported data.

The paper demonstrates per-step transition probability, not end-to-end automation reliability. Figure 4 shows that the on-neighbor strategy achieves approximately a 50% success rate per attempt. This is approximately twice the rate of alternatives, which is a meaningful improvement. However, the claim of "automated atomic manipulation" (title and abstract) requires the stronger demonstration that these per-step probabilities can be chained into reliable multi-step trajectories, and the paper provides only anecdotal (single-trajectory) evidence for this.

Does the paper validate that the learned probability model is accurate?

Not directly β€” and the paper is transparent about this. The paper explicitly acknowledges: "we do not have ground-truth data for the learned transition probabilities to quantitatively assess the accuracy of our predictions." The validation strategy is indirect: the model is validated through its use for control. If the model identifies beam positions that successfully cause transitions at a higher rate than alternatives, it must have captured something real about the underlying dynamics.

This is a reasonable validation strategy given the constraint β€” ground-truth transition probabilities for Si-on-graphene are not available from first-principles physics calculations that would be needed to independently verify the learned probability values β€” but it means the paper validates the policy (which beam position to choose) rather than the model (the full probability distribution over all beam positions and dwell times). A model that correctly identifies the optimal beam position but is systematically wrong everywhere else (e.g., the transition probability as a function of distance from the neighbor follows an incorrect functional form, but still peaks at the right location) would pass the control validation while having poor probability calibration. This distinction matters if the model is to be used for anything beyond greedy action selection β€” for example, planning trajectories under uncertainty, estimating expected manipulation time, or optimizing for multi-hop transitions.

Is the on-neighbor result a genuine discovery, or a confirmation of existing belief?

The paper presents it primarily as a confirmation. The abstract and introduction describe the on-neighbor finding as confirming "what was anecdotally held to be true" and "the physically intuitive, but heuristic, assumption." Section 5 states: "Our main finding confirms what was anecdotally held to be true by the microscopy community."

This framing is somewhat limiting. The paper does not explore whether the learned model reveals any non-intuitive spatial structure that was not previously suspected β€” for example, asymmetries in the transition probability contours, interactions between the beam position and the choice among symmetrically-equivalent neighbors, or the width of the probability peak around the neighbor position. The center panel of Figure 1 shows contours that appear roughly circular and centered on each neighbor, which is consistent with the intuitive knock-on picture, but the paper does not quantitatively characterize deviations from this simple picture. If the learned model contains richer structure (e.g., the optimal position is not exactly on the neighbor nucleus but slightly offset in a consistent direction, or the probability contours for different neighbors interact in non-trivial ways), this is not discussed.

The comparison with alternative beam placements in Figure 4 validates that the on-neighbor strategy is best among the five tested, but the tested alternatives (Short, Past, Perpendicular Offset) represent only a coarse sampling of the possible spatial deviations. A more thorough validation would systematically vary beam position in a grid around the neighbor to empirically map the transition probability surface and compare it against the learned model's predictions. The paper's synthetic evaluation framework (Section 6) does exactly this β€” evaluating learned models on a uniformly-spaced grid β€” but this is done only for synthetic data with known ground truth, not for the real system where the model's accuracy is most in question.

Is the synthetic evaluation framework sufficient to validate the learning algorithm?

It is well-designed for its purpose but has limited direct connection to the real system. The synthetic framework convincingly demonstrates that:

  1. The learning algorithm converges to accurate rate functions as data increases (Figure 6).
  2. The neural network outperforms classical alternatives (Figure 7, left).
  3. Ensemble distillation improves robustness (Figure 8, left).

However, the synthetic rate functions are mixtures of Gaussians β€” chosen because they "generalize the family of rate functions we expect to see in the real world." Whether the real rate function actually belongs to this family is precisely what is not known. If the real transition dynamics have sharp discontinuities, long-range correlations, or non-Gaussian spatial structure, the synthetic experiments would overestimate the learning algorithm's real-world performance.

The paper does not report experiments that bridge the synthetic and real evaluation regimes β€” for example, using the synthetic framework to predict how many real positive transitions would be needed for convergence, and then verifying that the real model's performance (as measured by controller success rate) improves according to that prediction as data accumulates. Such a bridging experiment would validate that the synthetic scaling laws are predictive of real-world learning behavior, but it would require a time series of models trained on progressively larger real datasets, which may not have been collected.

Are the reported confidence intervals adequate?

The 95% CI for the transition probability is extremely wide (0.246 to 0.754), spanning a factor of 3. This 50.8-percentage-point range reflects substantial uncertainty in the estimate of the on-neighbor success rate. The paper does not report the sample size used to compute this interval, but such a wide interval suggests either a relatively small number of trials or high inherent variability. This uncertainty propagates to any downstream use of the learned model: if the true transition probability is 0.25 versus 0.75, the expected number of attempts to complete a 5-step trajectory differs by a factor of 3, which has significant implications for throughput and beam-time planning.

The controller comparison results in Figure 4 are reported as point estimates without confidence intervals or error bars, making it impossible to assess whether the differences between strategies (e.g., On Neighbor at ~50% vs. Short of Neighbor at ~20%) are statistically significant or could be explained by sampling variability. Given the wide CI for the on-neighbor estimate, the alternatives likely also have substantial uncertainty, and some of the apparent differences between the below-25% strategies may not be statistically meaningful.

Missing experiments that would strengthen the paper

  • Trajectory-level statistics: Success rate over many attempted trajectories, distribution of steps-to-goal, failure modes (does the dopant ever get lost or move to unintended sites?).
  • Dwell-time sweep: The exponential CDF model predicts how transition probability varies with Ξ”t. Testing this prediction at a few dwell times (e.g., 1 s, 3 s, 5 s, 10 s) would validate the parametric form beyond the single 5-second condition.
  • Spatial grid sweep around the neighbor: Rather than only testing four offset directions (Short, Past, Perpendicular), placing the beam on a grid of positions around the neighbor and measuring the empirical transition rate would map the probability surface directly, providing a model-free validation of the learned contours.
  • Comparison against a physics-based model: If any first-principles estimate of knock-on cross-sections or transition rates exists for this system, comparing the learned model against that physics-based prediction would contextualize the data-driven approach's advantages (or reveal that it simply recovers what physics already predicts).
  • Cross-dopant or cross-substrate generalization: The model is trained and tested on the same Si-on-graphene system. Testing whether a model trained on one dopant atom transfers to a different dopant atom in a different region of the same graphene sheet would assess generalization, which is relevant for practical deployment (you would not want to retrain from scratch for every new dopant).

Conditional nature of the claims

The paper's central claim β€” that machine learning can estimate transition dynamics and enable automated atomic manipulation β€” holds under the specific conditions tested:

  • Single dopant on a pristine 3-fold coordinated graphene lattice.
  • Fixed beam current (90 pA) and dwell time (5 seconds).
  • One-hop targeting (the controller targets a specific neighbor, and multi-hop events are treated as incidental).
  • Hundreds of positive transitions available for training.
  • Careful alignment and filtering pipeline in place.

The paper is explicit about the first condition (Section 7: "The scenario we considered in this work is somewhat idealized: we limit ourselves to single dopant and 3-way lattices") but does not emphasize the others as strongly. The requirement of hundreds of positive transitions, documented in Section 6, implies that the method has a substantial data appetite that may limit its applicability to dopant-substrate systems where transitions are rare or dwell times must be kept short to avoid beam damage. The fixed beam current and dwell time mean that the learned model's temporal predictions (how probability scales with Ξ”t) have not been validated, even though the exponential CDF form makes specific predictions about this scaling.

6. Limitations and Trade-offs

The Pipeline Is Validated on a Single Dopant-Substrate System in an Idealized Configuration

The constraint. The entire empirical demonstration β€” data collection, model training, and automated control β€” is performed on exactly one physical system: a single silicon dopant atom on a pristine 3-fold coordinated graphene lattice with no defects, holes, or other dopants present. The paper is explicitly transparent about this, stating in Section 7:

"The scenario we considered in this work is somewhat idealized: we limit ourselves to single dopant and 3-way lattices for our learned dynamics."

The filtering pipeline (Section 4.3) actively enforces this idealization: examples where the dopant does not have exactly three neighbors are discarded (removing 3,593 examples, the largest single filter), and examples where neighbor positions do not approximately align with the idealized hexagonal lattice (average distance > 0.71 Γ… between corresponding neighbor pairs) are discarded (removing 411 more). This means the training data is selected precisely for conformity to the single-dopant, pristine-lattice ideal, and the model has never seen non-pristine configurations.

The consequence. The learned transition model cannot be assumed to generalize to any of the following practically important settings, none of which have been tested:

  • Multiple dopants: If two or more silicon atoms are present on the same graphene sheet, the beam could induce transitions in either dopant, or the dopants could interact (e.g., one dopant's presence altering the local electronic structure and thus the transition dynamics of the other). The transition model has no mechanism for modeling multi-dopant interactions because it was never trained on such data. The paper identifies this as future work (Section 7) but provides no evidence that the methodology extends naturally.

  • Non-pristine lattices with defects: The neighbor-count filter (Section 4.3) removed 3,593 examples (~53% of raw data) precisely because the detected neighbor count was not exactly three, indicating "non-pristine graphene" β€” likely carbon vacancies, Stone-Wales defects, grain boundaries, or other common lattice imperfections. A practical atomic fabrication task would inevitably encounter such defects, and the dopant's transition dynamics could differ substantially near them (different bonding environments, altered knock-on thresholds, different local strain fields). The model has zero training data from such configurations and would likely fail unpredictably.

  • 4-fold coordinated graphene (or other lattice geometries): The paper's entire coordinate standardization and augmentation pipeline (Section 4.3) assumes exactly three neighbors at 120Β° intervals, with rotation augmentation using exactly 0Β°, 120Β°, and 240Β°. Extending to a different lattice geometry (e.g., 4-fold square lattice) would require re-engineering the entire pipeline β€” new augmentation symmetries, new neighbor labeling, possibly a different parametric decomposition if the physical mechanisms differ. The paper does not discuss what aspects of the methodology are lattice-agnostic versus lattice-specific.

  • Different dopant species or substrate materials: Silicon on graphene is a specific chemical system. Transition dynamics for a different dopant atom (e.g., phosphorus, boron, nitrogen) on the same graphene lattice, or the same silicon dopant on a different substrate (e.g., hexagonal boron nitride, transition metal dichalcogenides), could differ qualitatively due to different atomic masses, binding energies, and electronic excitation cross-sections. The paper provides no evidence that the learned rate function for Si-on-graphene transfers even partially to other dopant-substrate combinations.

What evidence exists in the paper. The only direct evidence is the single successful trajectory (Figure 5) on the pristine Si-on-graphene system. The synthetic experiments (Section 6) test generalization of the learning algorithm across many synthetic rate functions, but all those experiments use the same idealized hexagonal lattice geometry with a single dopant β€” they test robustness to variation in the rate function shape, not to variation in the physical configuration (number of dopants, lattice defects, coordination number). The filtering statistics themselves (Section 4.3) reveal how frequently real data deviates from the idealized configuration: 80% of raw examples are discarded, with the largest fraction failing the neighbor-count criterion, demonstrating that non-ideal configurations are common in practice even when the experimental goal is a pristine single-dopant system.

Mitigation status. The paper acknowledges this limitation explicitly in Section 7: "Going forward, we will be exploring broader settings: multiple dopants, graphene with 4-way connections and aberrations (such as holes)." This is framed as future work, not as something addressed in the current paper. No experiments, even preliminary, are reported for these broader settings. The paper provides no principled argument for why the methodology should transfer β€” it simply states the intention to explore it. A practitioner reading this paper would have zero guidance on whether the approach is likely to succeed in non-idealized configurations, making it impossible to assess the method's practical scope without replicating the entire data collection and modeling pipeline for each new setting.

The Full Cost of Difficulty Estimation (Data Collection and Filtering Overhead) Is Not Factored Into Any Efficiency Claim

The assumption. The paper demonstrates that a learned model can identify optimal beam positions and enable automated control, but this demonstration rests on a substantial, unquantified upfront investment in data collection and curation that is never amortized or accounted for in any cost-effectiveness metric. The headline results β€” 50% transition success rate, successful five-step trajectory β€” are achieved after the model has been trained on thousands of experimental trials, each consuming 1–10 seconds of dwell time plus imaging overhead, representing many hours of dedicated STEM operation.

The consequence. A practitioner cannot evaluate the cost-benefit tradeoff of this approach versus alternatives. Consider three scenarios:

  1. Manual control by an expert microscopist: If an expert can achieve, say, a 30–40% per-step success rate through intuition and experience (the paper does not report this baseline, but the community's heuristic of "on neighbor" placement suggests experienced operators can achieve non-trivial success rates), then the automated approach's 50% rate represents a modest improvement β€” but the expert has zero upfront training cost. The data collection campaign (6,754 raw trials, ~20% yield after filtering) might exceed the total number of steps an expert would need for a specific fabrication task. The paper provides no comparison against human expert performance, making it impossible to assess when automation is worth the data collection investment.

  2. Physics-based modeling: If first-principles density functional theory (DFT) or molecular dynamics simulations could predict optimal beam positions with, say, 30–40% accuracy, the ML approach's 50% rate is an improvement β€” but the computational cost of running DFT simulations (days to weeks on a cluster) must be weighed against the experimental cost of collecting thousands of STEM trials (many hours of instrument time). The paper provides no such comparison, nor does it estimate the dollar cost of the data collection campaign.

  3. Deployment on a new dopant-substrate system: For each new chemical system, the entire data collection, alignment, filtering, and training pipeline must be repeated from scratch. The synthetic scaling experiments (Figure 6) indicate that several hundred positive transitions are needed for convergence, and the real-data experience suggests that achieving this requires several thousand raw trials (accounting for filtering losses and the fraction that are negative transitions). If each raw trial takes ~30 seconds (dwell time + imaging overhead), a campaign of 5,000 trials represents ~40 hours of continuous STEM operation β€” a substantial allocation of instrument time on a scarce, expensive resource. The paper provides no framework for estimating whether this investment is justified for a given application.

What evidence exists in the paper. Section 4.3 reports the starting dataset size (6,754 examples) and the number surviving filtering (1,953 examples, ~29%). The paper does not report the fraction of the 1,953 examples that are positive transitions, but given uniform beam position sampling within a 2.84 Γ… disk and the fact that transitions primarily occur when the beam is near a carbon neighbor (a small fraction of the disk area), the positive-transition fraction is likely in the 10–30% range. This implies that the effective training set contains on the order of several hundred positive transitions. The synthetic scaling experiments (Figure 6) show that models converge "once hundreds of positive transitions are available" β€” validating that the data volume was necessary, but also quantifying the data appetite of the approach.

The "Learned Rates (Less Data)" condition (Figure 4) provides indirect evidence of the data requirement: a model trained on approximately half the collected data (~500 positive transitions) produced an incorrect optimal beam position ("just past the neighbour"), resulting in dramatically worse control performance. This suggests that the final model's convergence was not guaranteed until the full dataset was accumulated, meaning the data requirement is closer to the upper end of the "hundreds" range.

Critically, the paper makes no attempt to report the total instrument time, the dollar cost, or the number of experimental sessions required for data collection. There is no efficiency claim of the form "the data collection cost is amortized over X fabrication steps" or "the approach becomes cost-effective after Y trajectories." The 50% success rate is presented as a standalone result without any denominator in terms of the upfront investment required to achieve it.

Mitigation status. Not addressed. The paper does not discuss data efficiency, cost amortization, or break-even analysis anywhere. The synthetic scaling experiments (Section 6) provide some guidance about how much data is needed (hundreds of positive transitions), but this is presented as a characterization of the learning algorithm's behavior rather than as a cost analysis. The paper does not propose any method for reducing the data requirement (e.g., active learning to focus data collection on high-information beam positions, transfer learning from one dopant to another, or incorporating physical priors to reduce sample complexity). A practitioner reading this paper would know approximately how much data is needed but would have no framework for deciding whether that data collection is worth the cost for their specific application.

The Transition Model's Temporal Predictions and Dwell-Time Dependence Are Entirely Unvalidated

The assumption. The paper's parametric model (Section 4.4) decomposes the transition probability as an exponential cumulative distribution function $P(S' \neq s_0 \mid s_0, a) = 1 - e^{-\lambda \Delta t}$. This form encodes a strong assumption: that the transition rate $\lambda$ is constant over time (the memoryless property), and that the probability of a transition scales with dwell time $\Delta t$ according to this specific functional form. This assumption is motivated by the physical constraint that "the probability of moving to another state should be monotonically increasing in $\Delta t$" (Section 4.4), and the exponential CDF is the simplest parametric form that guarantees this monotonicity. However, the actual physical process β€” knock-on damage, ionization, sputtering β€” may not follow an exponential time dependence. For example, if there is an incubation period before damage accumulates, or if the damage rate changes as the local electronic structure is modified by the beam, the true time dependence could be sigmoidal, power-law, or multi-exponential.

The consequence. All controller experiments (Section 5) use a constant 5-second dwell time at 90 pA beam current. The learned model's predictions for other dwell times β€” 1 second, 10 seconds, 0.5 seconds β€” are entirely unvalidated against experimental data. If the true time-dependence deviates from the exponential CDF form, then:

  • For shorter dwell times: The model might systematically overestimate or underestimate transition probability. If the true process has an incubation threshold (no transitions occur below some minimum dose), the exponential CDF would predict small but non-zero probabilities at very short dwell times, leading to overoptimistic expected success rates. Conversely, if the true rate accelerates over time (damage accumulation), the exponential CDF's assumption of constant instantaneous rate would underestimate long-dwell-time probabilities.

  • For longer dwell times: Multi-hop transitions (as observed in the first step of Figure 5) become more likely, but the current model only predicts single-hop outcomes. The exponential CDF gives the probability of any transition occurring, but the model's categorical distribution $y$ over which neighbor is chosen is only trained on single-hop outcomes. If the dopant can hop multiple times within a single dwell period, the actual next-state distribution may differ substantially from the single-hop distribution, and the model has no way to represent this.

  • For dose-equivalent variations in beam current: The paper converts dwell time to electron dose (5 seconds at 90 pA β‰ˆ 3 billion electrons), implying that dose is the physically relevant quantity. However, the model treats $\Delta t$ as an input but does not separately parameterize beam current. If dose rate matters (e.g., a short, intense pulse produces different damage than a long, weak one delivering the same total electrons), the model cannot capture this because beam current is held constant and never varied in the training data.

What evidence exists in the paper. The only dwell-time-related evidence is:

  • The data collection protocol varied dwell times from 1 to 10 seconds (Section 4.1, top-left panel of Figure 3 showing the histogram). This means the training data contains transitions at different dwell times, and the exponential CDF fit averages over this variation. However, the model's accuracy at predicting how probability changes with $\Delta t$ is never evaluated β€” the synthetic experiments (Section 6) evaluate spatial predictions (MSE over beam positions) and argmax identification (regret), but do not include dwell-time-specific metrics.
  • The first step of the automated trajectory (Figure 5) resulted in a multi-site jump, which the paper attributes to the absence of real-time feedback β€” the beam continued for the full 5 seconds after the dopant had already hopped once, causing additional transitions. This observation directly implicates the dwell-time model: if the exponential CDF model were perfectly accurate and the controller knew exactly when the first transition occurred, it could stop the beam to prevent subsequent unintended hops. The fact that multi-hop events occur at all suggests that 5 seconds is sufficient for multiple transitions, which the current model cannot predict or control.

There is no experiment where dwell time is systematically varied (e.g., measuring transition success rate at 1s, 3s, 5s, 10s for the same beam position) and compared against the exponential CDF predictions. Such an experiment would directly validate or invalidate the parametric form.

Mitigation status. The paper does not address this limitation or propose validation experiments for the temporal model. The exponential CDF form is justified only by the monotonicity constraint ("the probability of moving to another state should be monotonically increasing in $\Delta t$") and the citation to Voter (2007) on kinetic Monte Carlo methods, which is a modeling convention rather than a physical validation for this specific system. The paper's use of a constant 5-second dwell time for all controller experiments effectively sidesteps the question of whether the dwell-time dependence is correctly captured. A practitioner could use the model to predict, say, the success probability at a 2-second dwell time, but would have no experimental evidence that this prediction is reliable.

Real-Time Feedback Is Absent, Limiting Both Throughput and Control Precision

The constraint. The automated controller described in Section 5 operates in an open-loop fashion with respect to transition detection: it fires the beam for a fixed 5-second dwell time and only checks whether a transition occurred after the dwell period completes, by acquiring a new image and running atom detection. It does not use real-time detector feedback to determine when the dopant has actually moved and terminate the beam early. The paper explicitly identifies this as a limitation:

"Real-time detector feedback was not used to indicate if the silicon transitioned earlier than the designated dwell time, and therefore this was one limitation in the current work."

The consequence. This design choice has three direct consequences, all evidenced in the single trajectory shown in Figure 5:

  1. Unintended multi-hop transitions: The first beam pulse in Figure 5 caused the dopant to jump multiple lattice sites rather than the single intended hop. The paper explains this as a consequence of the beam continuing to fire after the first transition had already occurred β€” the dopant moved to a neighbor, the beam (still on for the remainder of the 5-second period) continued to stimulate that neighbor, and the dopant hopped again. From the controller's perspective, this is an error: it intended a single hop along the shortest path, and instead got a multi-hop that placed the dopant at an unplanned location (requiring the subsequent steps to recover toward the goal). The paper presents this optimistically as a feature that "can be exploited for more efficient beam manipulation," but from a control-reliability standpoint, unpredictable multi-hop events reduce precision and make trajectory planning unreliable.

  2. Wasted beam dose and potential sample damage: For all trials where the transition occurs before the full 5-second dwell time elapses, the remaining beam exposure is unnecessary and potentially damaging. This excess dose could cause unintended additional transitions (as observed), create lattice defects (knocking out carbon atoms), or contaminate the sample. The paper does not quantify how often transitions occur before 5 seconds, so the magnitude of this wasted dose is unknown, but it represents a fundamental inefficiency: the controller is applying more dose than needed for each step, which is both slower (longer effective step time) and more damaging than a feedback-controlled approach would be.

  3. Reduced effective throughput: The fixed 5-second dwell time sets a lower bound on per-step latency. If transitions typically occur after, say, 1–2 seconds of beam exposure, a feedback-based controller could terminate the beam and proceed to the next step immediately, achieving 2.5–5Γ— faster manipulation speed. The paper's vision of "hundreds of fabrication steps per second" (Section 7) is fundamentally incompatible with fixed 5-second dwell times β€” achieving that throughput would require dwell times on the order of milliseconds, which in turn would require real-time transition detection to know when each hop has completed.

What evidence exists in the paper. The multi-hop first step in Figure 5 is the direct evidence. The paper does not report how frequently multi-hop events occur across all controller trials, whether the multi-hop rate depends on beam position (e.g., does placing the beam on the neighbor sometimes cause a double-hop while placing it short of the neighbor causes only single hops?), or whether there is a systematic relationship between dwell time and the probability of multi-hop events. The histogram of dwell times (Figure 3, top-left) shows that training data included dwell times from 1 to 10 seconds, so the training data presumably contains some multi-hop transitions (where the dopant moved twice within a longer dwell period), but these are not explicitly identified or analyzed in the paper.

Mitigation status. The paper acknowledges the limitation explicitly but proposes no technical solution. The statement that real-time feedback "was not used" implies it is technically feasible (the atom detection neural networks from Ghosh et al. (2021) are described as operating "in as close to real time as possible"), but the paper does not implement it or discuss the engineering challenges involved (e.g., the latency of image acquisition, image processing, and atom detection versus the timescale of dopant motion). The paper also speculates that multi-hop behavior "can be exploited for more efficient beam manipulation," but provides no controller design, model extension, or experimental demonstration of such exploitation. This remains entirely aspirational.

Controller Reliability Is Characterized Only by Per-Step Success Rate, Not by End-to-End Trajectory Statistics

The constraint. The paper's experimental validation of automated control (Section 5) reports exactly one aggregate statistic: the per-step transition success rate for each beam-placement strategy (Figure 4), with the on-neighbor strategy achieving approximately 50%. The paper also shows exactly one complete trajectory (Figure 5) as a qualitative demonstration. No statistics are reported for end-to-end control performance β€” how often the controller successfully drives the dopant from start to goal, how many beam pulses are required on average, what failure modes occur, or whether the controller ever loses the dopant entirely.

The consequence. A per-step success rate of 50% does not directly translate to end-to-end reliability, and the missing statistics matter for assessing practical utility:

  • Expected number of attempts per trajectory: For a trajectory of N steps with per-step success probability p, the expected number of total beam pulses depends on the retry strategy. If the controller simply retries each failed step until it succeeds (implied by "until the dopant has arrived at the goal position, or until we have reached the maximum allowable attempts"), and each attempt is independent, the expected number of pulses per step is 1/p, and the total expected pulses for the trajectory is N/p. For p = 0.5 and a modest N = 5 trajectory, this is 10 pulses β€” but some trajectories will require many more. The paper does not report the actual distribution of pulses-per-step or pulses-per-trajectory.

  • Probability of catastropic failure: The paper does not characterize what happens when a transition fails. Does the dopant typically stay in place (a "null" outcome, requiring a retry), or does it sometimes move to an unintended neighbor (a "mistake" outcome, requiring the controller to replan from a new position)? If unintended moves occur β€” which they almost certainly do, since the learned model's categorical distribution $y$ assigns non-zero probability to all three neighbors even at the optimal beam position β€” then the dopant can wander off the shortest path, lengthening the trajectory or, in the worst case, moving out of the field of view or into a defective region where the model's predictions are unreliable. The paper reports no statistics on unintended transition frequency or direction.

  • Controller robustness to detection failures: The atom detection neural networks (Ghosh et al., 2021) are described as "fast and robust even to out of distribution effects," but the filtering pipeline (Section 4.3) discarded 4 examples because the dopant count was not exactly one before and after the transition, and 3,593 examples because the neighbor count was not exactly three. These failures occurred during offline data processing, but similar detection failures could occur online during automated control. If the controller misidentifies the dopant's position, it will place the beam at the wrong location, potentially causing unintended transitions or failing to cause any transition at all. The paper provides no characterization of online atom detection reliability or the controller's behavior under detection noise.

  • Multi-hop events as a control challenge: As discussed in the previous limitation, multi-hop events occur (evidenced by Figure 5) and the current model cannot predict them. The controller's replanning capability after a multi-hop (i.e., detecting that the dopant is now at an unexpected location and computing a new shortest path to the goal) is not characterized. The single trajectory in Figure 5 shows that the controller successfully recovered from the initial multi-hop and completed the task in the remaining four steps, but this is an anecdote, not a statistic.

What evidence exists in the paper. The only trajectory-level evidence is the single five-step trajectory in Figure 5. The paper does not report:

  • The number of trajectories attempted.
  • The number of successful trajectories (reached the goal within the maximum allowable attempts).
  • The distribution of total beam pulses per trajectory.
  • The frequency or direction of unintended transitions.
  • Any instances of the controller failing to reach the goal or losing the dopant.

The per-step success rate (Figure 4) provides a lower bound on trajectory reliability: if each step has a 50% chance of the intended transition occurring, and unintended transitions can move the dopant in wrong directions, the probability of completing a 5-step trajectory without any deviation from the plan is at most (0.5)^5 β‰ˆ 3%, implying that replanning and retry logic is essential. The controller presumably implements such logic (it would be inoperable otherwise), but its design and performance are not described.

Mitigation status. Not addressed. The paper treats the single trajectory in Figure 5 as a proof-of-concept demonstration, and the per-step success rate in Figure 4 as the primary quantitative validation. The transition from per-step to trajectory-level reliability is never discussed, and no trajectory-level statistics are reported. Given that the paper's stated goal is "automated atomic manipulation" (title and abstract), the absence of end-to-end controller characterization is a significant gap β€” a practitioner cannot assess whether the system is reliable enough for their fabrication task or how many beam pulses (and how much instrument time) a typical manipulation would require.

The Methodology Requires Repeated, High-Quality Imaging of the Same Sample Region, Which May Not Be Feasible for Beam-Sensitive or Contamination-Prone Materials

The assumption. The entire pipeline β€” data collection, alignment, filtering, and online control β€” depends on the ability to repeatedly image the same graphene region, detect atomic positions, and correlate them across time steps. Each trial involves acquiring two images (before and after the beam pulse), and the automated controller images after each step to determine the outcome. This means the sample region of interest is imaged many times: 6,754 trials for data collection (Γ—2 images each = ~13,500 images) plus however many steps are needed for each control trajectory.

The paper acknowledges that "image acquisition is done using the same electron beam, which implies that imaging itself can cause a transition; to mitigate this, the imaging electron dose should be minimized" (Section 4.1). However, this mitigation has limits: there is a trade-off between minimizing imaging dose (to avoid unintended transitions) and maintaining sufficient image quality for reliable atom detection (to avoid misidentifying atomic positions).

The consequence. The approach assumes that the sample can tolerate extensive imaging without unacceptable degradation. For the specific Si-on-graphene system studied, this assumption appears to hold (the paper successfully collected and processed thousands of images). However, this property is not universal:

  • Beam-sensitive materials: Many materials of interest for atomic fabrication β€” organic molecules, biological specimens, certain 2D materials beyond graphene β€” are substantially more beam-sensitive than graphene. They may undergo structural changes, mass loss, or chemical decomposition at cumulative electron doses far below what this study's data collection protocol required. The paper provides no guidance on how to adapt the methodology for dose-sensitive materials, or what the minimum imaging dose is for reliable atom detection (the atom detection networks presumably have some minimum signal-to-noise requirement, but this is not quantified).

  • Contamination during extended imaging: Repeated imaging of the same region can lead to hydrocarbon contamination (residual gasses in the microscope column being cracked by the electron beam and deposited on the sample surface), which could alter the local chemical environment and thus the transition dynamics. The paper does not discuss contamination effects or whether they were observed during the extended data collection campaign.

  • Drift accumulation over long experiments: While the convolutional aligner (Section 4.2) corrects for drift between consecutive image pairs, it may not handle large cumulative drift over the course of a multi-hour data collection session. If the sample drifts substantially, the field of view may shift away from the dopant, or the same region may experience different beam conditions (e.g., the beam may pass through different thicknesses of the sample, altering the effective dose). The paper does not report the total duration of data collection or the magnitude of cumulative drift.

What evidence exists in the paper. The paper provides indirect evidence that imaging-induced damage was manageable for this system: they successfully collected 6,754 trials, filtered to 1,953 clean examples, and trained a working model. The fact that imaging dose was "minimized" (Section 4.1) suggests the authors were aware of the trade-off and took steps to manage it, but no quantitative values are reported for the imaging electron dose, the signal-to-noise ratio of the resulting images, or the atom detection accuracy as a function of imaging dose.

The filtering statistics provide limited insight into imaging-related data loss: 4 examples were discarded for incorrect dopant count (possibly due to imaging quality issues causing misdetection), and 3,593 examples were discarded for neighbor count violations (which could be caused by genuine lattice defects, beam-induced damage during data collection, or detection failures due to poor image quality). The paper does not distinguish between these causes, so the fraction of data loss attributable to imaging quality versus genuine physical non-ideality is unknown.

Mitigation status. Partially addressed by the design choice to minimize imaging dose (Section 4.1), but this mitigation is not quantified and its limits are not explored. The paper does not report what happens if imaging dose is reduced further (e.g., does atom detection accuracy degrade to an unacceptable level?), or what the maximum tolerable cumulative dose is for this system. For a practitioner considering applying this methodology to a different material, the paper provides essentially no guidance on how to assess whether their material can tolerate the required imaging load, or how to optimize the imaging-dose vs. detection-accuracy trade-off. This is a significant practical barrier to adoption because the imaging requirement is not incidental to the method β€” it is fundamental to both the data collection and control loops, and if a material cannot survive it, the entire approach is infeasible.

7. Implications and Future Directions

How This Work Changes the Landscape

A methodological reframing, not a physical discovery. The paper's primary impact on the microscopy and atomic manipulation community is not the confirmation that on-neighbor beam placement is optimal β€” that was already the community's heuristic β€” but rather the demonstration that an end-to-end data-driven pipeline can replace physical intuition with a quantified, operational probability model capable of driving closed-loop automation. This shifts the field's conceptual default from "we need better physical models to control beam-induced dynamics" toward "we need systematic data collection campaigns and careful data engineering to learn the transition function empirically." The magnitude of this shift should not be overstated: it is a methodological contribution to how atomic manipulation is studied and automated, not a discovery of new physics or a qualitatively new manipulation capability. The Si-on-graphene system was already manipulable by experts; the paper makes it manipulable by an automated controller with quantified success probabilities.

The paper resolves a specific, previously fuzzy question in the community: is the optimal beam position for inducing a silicon dopant transition exactly on the neighboring carbon atom, or somewhere else? Prior work relied on anecdotal evidence and physical intuition (knock-on momentum transfer) to support the on-neighbor hypothesis, but no one had measured it quantitatively or mapped the probability surface as a function of beam position. The paper provides the first direct measurement: 50.0% success rate at 5 seconds, 90 pA, with a 95% CI of 0.246 to 0.754 (Section 5). Alternative spatial offsets (short of neighbor, past neighbor, perpendicular offset) all fall below 25%. This converts a community belief into a quantified parameter, which is a useful but incremental advance β€” it confirms what was suspected rather than overturning it.

The pipeline, not the model, is the reusable contribution. The paper's most durable impact is likely to be the data engineering methodology (Sections 4.2–4.3) rather than the specific neural network architecture. The alignment CNN, the iterative drift correction protocol, the filtering criteria and their quantified yields, and the rotation/reflection augmentation that encodes hexagonal lattice symmetry β€” these components together form a template that can be adapted to other dopant-substrate systems. The fact that the learning algorithm itself is a three-layer network with standard ReLU activations makes the point implicitly: the intellectual heavy lifting is in the data pipeline, not the model architecture. This inverts the typical ML research priority and provides a concrete example of what "data-centric AI" looks like in a scientific instrumentation context.

Regret vs. MSE reframes evaluation for control tasks. The paper introduces (or at least, prominently applies) the distinction between prediction accuracy (MSE) and decision quality (regret) in a microscopy automation context. The empirical finding that MSE converges faster than regret as a function of dataset size (Figure 7, right) has a sharp practical implication: a model whose rate function looks visually correct (low MSE) can still have a substantially wrong argmax (high regret), and therefore produce a controller that fails. This explains the paper's own internal narrative β€” the "Learned Rates (Less Data)" model produced rate functions that looked qualitatively similar to the final model but whose optimal beam position ("just past the neighbour") was different enough to cause a 2Γ— drop in transition success rate (Figure 4). This insight is portable to any domain where a learned model is used for action selection rather than prediction, and it provides a concrete diagnostic: track regret (or controller success rate) rather than prediction loss when deciding if you have enough data.

Directions that become more attractive. The paper makes empirical, data-driven transition modeling the obvious next step for any atomic manipulation system where the physical mechanisms are complex or poorly understood. Specifically: (1) building similar pipelines for other dopant species (phosphorus, boron, nitrogen) on graphene; (2) extending the approach to other 2D substrates (hexagonal boron nitride, transition metal dichalcogenides) where the lattice symmetry differs; (3) incorporating active learning to reduce the data collection burden by focusing beam pulses on high-uncertainty or high-information regions of the position-dwell-time space. The synthetic framework (Section 6) provides a reusable evaluation harness for testing algorithmic improvements (better architectures, active sampling strategies, transfer learning) before committing expensive microscope time.

Directions that become less attractive. The paper implicitly argues against approaches that prioritize physical modeling over data collection. If the transition dynamics can be learned adequately from ~2,000 clean examples (with hundreds of positive transitions) using a simple neural network, then efforts to build highly accurate first-principles models of knock-on, ionization, and sputtering for the purpose of predicting optimal beam positions become less urgent β€” at least for systems where systematic data collection is feasible. Physical modeling remains essential for understanding why transitions occur and for predicting behavior in regimes where data collection is impossible (e.g., extreme temperatures, novel dopant-substrate combinations not yet synthesized), but for the specific engineering task of automated control, the paper suggests that data beats theory in terms of actionable accuracy per unit effort.

The paper also weakens the case for manual, human-in-the-loop atomic manipulation as a scalable approach. The demonstrated automated trajectory (Figure 5), even with its limitations (open-loop dwell, multi-hop first step), shows that a controller operating at 50% per-step success rate and 5 seconds per attempt can complete a five-step trajectory without human intervention. Scaling this to higher throughput β€” by adding real-time feedback to terminate the beam early, optimizing dwell time, and incorporating multi-hop prediction β€” would widen the gap between automated and manual control, making continued reliance on expert operators increasingly difficult to justify for repetitive fabrication tasks on well-characterized systems.

A template, not a turnkey solution. It is important not to overstate the paper's immediate impact. The methodology is validated on exactly one physical system (Si on pristine 3-fold graphene) with one beam current (90 pA) and one dopant atom. The filtering statistics reveal that 80% of raw data was discarded, the majority because the local environment did not conform to the pristine single-dopant ideal. This means the pipeline as implemented is highly sensitive to configuration β€” it works on clean, idealized data and rejects everything else. Extending it to non-pristine lattices, multiple dopants, or different coordination geometries will require re-engineering significant portions of the pipeline (new augmentation symmetries, new filtering criteria, possibly new model architectures or loss functions). The paper opens this direction but does not travel down it. The landscape has shifted from "can we learn transition dynamics?" (answered: yes, for this system) to "how general is this methodology, and what does it cost to apply to a new system?" (unanswered).

Follow-Up Research This Work Enables

Real-time feedback control with early beam termination. The paper explicitly identifies the absence of real-time transition detection as a limitation and observes that the first step of the automated trajectory (Figure 5) caused a multi-site jump because the beam continued firing after the dopant had already hopped. A clear follow-up is to integrate the atom detection networks (Ghosh et al., 2021) into a closed-loop system that monitors the dopant position during the beam dwell period, terminating the beam within milliseconds of a detected transition. The key experiment would measure: (1) the latency distribution of transition detection (image acquisition + processing + atom identification time), (2) the probability of multi-hop events as a function of post-transition beam continuation time, and (3) the resulting improvement in single-hop precision (fraction of beam pulses that produce exactly one hop to the intended neighbor). If the detection latency is below ~100 ms and the typical time between successive hops is substantially longer, a feedback controller could eliminate most unintended multi-hop events while also reducing the total electron dose per successful transition (since the beam would be on only until the hop occurs, not for the full 5 seconds). This directly addresses the throughput limitation β€” "hundreds of fabrication steps per second" (Section 7) is only conceivable with sub-millisecond transition detection.

Systematic dwell-time sweep to validate the exponential CDF model. The transition model assumes a parametric form P(transition)=1βˆ’eβˆ’Ξ»Ξ”tP(\text{transition}) = 1 - e^{-\lambda \Delta t}, but this assumption is entirely unvalidated because all controller experiments use a fixed 5-second dwell time (Section 5). A targeted experiment would measure the empirical transition success rate at the on-neighbor beam position for dwell times spanning, say, 0.5 s, 1 s, 2 s, 3 s, 5 s, 7 s, and 10 s (at constant 90 pA beam current), with sufficient trials at each dwell time to estimate the probability with confidence intervals comparable to the reported 95% CI (0.246–0.754). Plotting the empirical probabilities against the exponential CDF fit would directly test whether the memoryless assumption holds. Deviations β€” for example, a sigmoidal curve implying an incubation threshold, or a saturation below 1.0 implying a non-zero probability of never transitioning β€” would motivate richer parametric forms (Weibull, log-normal, or multi-exponential) and would have direct implications for dwell-time optimization. If the exponential model fails, the optimal dwell time for maximizing transitions-per-unit-time (throughput) could differ substantially from what the current model predicts.

Extension to multi-dopant systems and non-pristine lattices. The paper's single-dopant, pristine-lattice scope is explicitly acknowledged as idealized (Section 7). The most important stress test is to repeat the entire pipeline β€” data collection, alignment, filtering, model training, and control β€” on a sample with two silicon dopants in close proximity (within a few lattice spacings). The key questions: (1) Can the model learn to predict which dopant moves when the beam is placed at different positions between them? (2) Does the presence of a second dopant change the transition probability surface for the first (e.g., due to altered local strain or electronic structure)? (3) Can a controller selectively move one dopant without disturbing the other? The filtering pipeline would need modification: the neighbor-count criterion (exactly three neighbors per dopant) would still apply, but the "exactly one dopant" filter would need to be relaxed to "exactly N dopants," and the output space would expand to include which dopant moved (or both, in correlated transitions). The synthetic evaluation framework (Section 6) provides a natural starting point: generate synthetic rate functions for two-dopant systems, verify that the learning algorithm can recover them, then move to real data collection. A negative result β€” e.g., the model fails to learn reliable transition dynamics even with substantially more data, or the controller cannot achieve selective single-dopant manipulation β€” would establish a fundamental limitation of the purely empirical approach and suggest that physical modeling (dopant-dopant interactions) may be necessary when multiple dopants are present.

Active learning to reduce the data collection burden. The paper's data collection protocol uses uniform random sampling of beam positions within a 2.84 Γ… disk (Section 4.1), which is simple but inefficient: most sampled positions are far from any carbon neighbor and produce only negative transitions, yielding little information about the rate function's spatial structure. The filtering pipeline discards 80% of raw data. A natural improvement is to use active learning: start with a small dataset (e.g., 100 random trials), train an initial model, and then use the model's uncertainty estimates (from the ensemble, Section 4.4) to select the next beam positions β€” sampling more densely in regions where the ensemble disagrees (high uncertainty) or where the predicted transition probability is high (exploitation). The synthetic framework (Section 6) enables systematic comparison: generate a synthetic rate function, run active learning versus random sampling at equivalent total trial budgets, and measure which reaches a target regret threshold in fewer trials. The key metric is the reduction in required positive transitions (or total trials) to achieve a controller with, say, β‰₯40% per-step success rate. If active learning reduces the data requirement by 2–3Γ—, it would directly address the practical cost barrier identified in the paper's implicit data budget (Section 6, Figure 6 suggests at least several hundred positive transitions, translating to thousands of raw trials). A negative result β€” active learning provides minimal benefit because the transition probability surface is too simple (a single Gaussian peak per neighbor) β€” would actually be informative: it would mean the uniform random sampling protocol is already near-optimal for this system, and the filtering loss (80%) is an unavoidable consequence of beam-sensitive detection, not a sampling inefficiency.

Cross-dopant and cross-sample transfer learning. The paper trains and tests on the same Si-on-graphene system. A practically crucial question is whether a model trained on one dopant atom transfers to a different dopant atom in a different region of the same graphene sheet, or to a different dopant atom in a separately prepared sample. The experiment: collect a full training dataset on dopant A (region 1), collect a much smaller dataset on dopant B (region 2, or a different sample), and compare three strategies β€” (a) train from scratch on dopant B's limited data, (b) fine-tune the dopant A model on dopant B's data, and (c) use the dopant A model directly on dopant B without fine-tuning. The metric is controller success rate for each strategy. If fine-tuning works with a fraction of the data required for from-scratch training (e.g., 50–100 positive transitions instead of 500+), it would demonstrate that the learned rate function captures dopant-invariant features (the lattice geometry, the general spatial structure of knock-on probability) and only needs modest adaptation for dopant-specific details (the exact peak width, the maximum rate). If direct transfer fails entirely (strategy c performs at chance level), it means the learned model is highly specific to the individual dopant and its local environment, and each new fabrication target requires a full data collection campaign. This result would substantially limit the practical scalability of the approach for applications requiring manipulation of many dopants across a large sample.

Physics-informed model comparison and hybrid approaches. The paper's model is purely empirical β€” it makes no reference to physical mechanisms beyond the exponential CDF monotonicity constraint. A valuable follow-up would be to compare the learned rate function against predictions from first-principles simulation (e.g., density functional theory or molecular dynamics calculations of knock-on cross-sections for Si in graphene). The comparison would quantify where the empirical model agrees with physics (e.g., the Gaussian-like spatial decay of transition probability with distance from the carbon neighbor) and where it deviates (e.g., asymmetries in the probability contours that physics attributes to the specific bonding direction or anisotropic momentum transfer). If the deviations are systematic and predictable, a hybrid model could incorporate physical priors (e.g., using the simulated cross-section as a mean function for a Gaussian process, or as a pretraining target for the neural network) to reduce the data requirement. The key experiment: pretrain the transition model on synthetic data generated from a physics simulation (not from random mixture-of-Gaussian rate functions), then fine-tune on limited real data, and compare the data efficiency against training from scratch on real data alone. If physics-informed pretraining reduces the required positive transitions by 5–10Γ—, it would provide a principled path to applying the methodology to dopant-substrate systems where extensive data collection is impractical (e.g., rare or radioactive dopants, samples that degrade quickly under the beam).

Practical Applications and Downstream Use Cases

Automated fabrication of dopant arrays for quantum devices. The paper's most direct application is in the fabrication of precisely positioned dopant arrays in 2D materials β€” a building block for solid-state quantum computing architectures, single-atom transistors, and quantum sensing devices. The demonstrated 50% per-step success rate (Figure 4) and automated trajectory (Figure 5) mean that moving a dopant across, say, 10 lattice sites would require approximately 20 beam pulses on average (at 50% success per attempt, with retries), consuming roughly 100 seconds of beam time at 5 seconds per pulse. With real-time feedback (eliminating unnecessary post-transition beam exposure), the per-pulse time could drop substantially if most transitions occur within the first 1–2 seconds. For a device requiring precise placement of 5–10 dopants, the total fabrication time on a single instrument would be on the order of tens of minutes to a few hours β€” within the range of a dedicated experimental session. The key advantage over manual operation is reproducibility: the same controller can execute the same task identically on multiple samples, with quantified success probabilities and no operator-to-operator variability. This is particularly relevant for quantum device fabrication, where dopant placement precision directly affects qubit coupling strengths and coherence times.

Training data generation for machine learning interatomic potentials. The methodology's byproduct β€” thousands of curated, aligned before/after image pairs with labeled transition outcomes β€” constitutes a valuable dataset for training or validating machine learning interatomic potentials (MLIPs) that model beam-induced dynamics. MLIPs are increasingly used to simulate atomic-scale processes at speeds approaching classical force fields while maintaining near-DFT accuracy, but they require large quantities of training data, typically from expensive first-principles calculations. The paper's dataset provides an experimental complement: real transition observations can serve as validation targets for MLIP predictions of Si hop probabilities in graphene, or can be used directly (through an inverse modeling approach) to fit parameters of a simplified physical model. The filtering statistics (80% discard rate, with 53% of raw data failing the neighbor-count criterion) also provide a diagnostic for simulation: if an MLIP predicts frequent non-pristine configurations or coordination number changes under the electron beam, it should reproduce the observed frequency of such events in real STEM data.

Benchmarking human expert performance against automated control. The paper's controller provides a quantitative baseline β€” 50% per-step success rate at 5-second dwell β€” that can be used to benchmark human operator performance on the same task. A simple experiment: have several expert microscopists attempt to move a silicon dopant along a specified shortest path using their best judgment for beam placement, measure their per-step success rate, total time, and trajectory accuracy, and compare against the automated controller. If expert performance is comparable (say, 40–60% success rate), the primary advantage of automation is throughput (eliminating human reaction time and decision latency) and scalability (one operator cannot control multiple microscopes simultaneously). If expert performance is substantially lower (say, 20–30%), it means the community's heuristic understanding was less precise than believed, and the data-driven approach provides a genuine improvement in capability, not just speed. Either outcome is valuable: the former justifies automation for economic reasons, the latter for performance reasons. The paper does not report this comparison, but the controller provides the quantitative baseline needed to design it.