Where the room is: photons, engineering and the next order of magnitude

On 16 October 2026 a fused Triton kernel on an NVIDIA A100 finished one velocity scan of a synthetic stack in 0.30 seconds. The stack had 1,024 exposures of a 256 × 256 pixel field and 4,225 trial velocities. The best conventional kernel in the same benchmark kit, a tiled gather, took 1.79 seconds. That is 5.9 times faster, close to the order of magnitude this book has been looking for. Then came the arithmetic that every chapter of this book recommends. The tiled gather was not limited by memory bandwidth. It was limited by double-precision coordinate arithmetic and branching. A gather that simply streamed its data at the card’s bandwidth, with no reuse at all, would have taken about 0.52 seconds. Against that ideal, the tensor-core kernel was about 1.7 times faster, and only on the workload most favourable to it (Chapter 40).

Nothing in the measurement was wrong. The numerator was real and the kernel was correct to half-precision accuracy. What changed was the denominator. This chapter is about that change, at the scale of the whole book. Forty-one chapters have each closed with a section asking the same question: what could a new method change here, and which limits are physical? The answers have a shape. A few limits recur in every field and no computer moves them. Many more are engineering, and some of those have been moved by factors of a hundred or more, usually by a change of representation and rarely by new hardware. And a narrow set of places remains where an order-of-magnitude gain in compute at equal sensitivity is plausible but not yet shown. The aim here is to say which is which, with the evidence for each claim stated at its actual strength, and to end with a programme of experiments that would settle the open cases.

Three kinds of limit

A model that covers almost everything

Almost every search in this book can be written in one local form. Let $d$ collect the data, whether pixels, light-curve samples, velocities or timing residuals. Then

where $h(\theta)$ is a unit-amplitude template for a planet with parameters $\theta$ (a trajectory, an orbit, a period), $F$ its amplitude, $X\beta$ a set of linear nuisance terms (a static sky, a trend, a stellar activity basis) and $C$ the noise covariance. Profiling out $\beta$ leaves the residual precision operator

and, with the book’s notation from Chapter 1, the two numbers that summarise the evidence at $\theta$:

For moving objects with independent pixel noise, $A$ and $B$ are the sums of the likelihood images $\psi_i$ and $\phi_i$ along the trajectory. For a transit they are sums over in-transit samples. For a radial-velocity planet they are inner products with a Keplerian under a Gaussian-process covariance. The structure is the same (Chapter 1, §“Two images that hold everything”).

Two properties of this form decide most of what follows. First, for independent groups of data $s$ (nights, sectors, seasons) and a template with a common amplitude, the pairs $(A_s,B_s)$ are sufficient:

Any hierarchy that keeps signed $(A_s,B_s)$ pairs and combines them along a correct trajectory loses nothing. Replacing them by $\sum_s\nu_s^2$, keeping only positive peaks, or requiring each segment to pass a threshold changes the hypothesis and loses sensitivity. In the project’s design studies, summing per-night powers instead of signed sums lost 0.15, 0.27 and 0.47 mag at 10, 30 and 100 nights (unpublished modelling; the general argument is in Chapter 37). Second, $B$ matters as much as $A$. A fast numerator with an approximate denominator is a different statistic. At an eight-sigma threshold, a 1% error in the assumed noise standard deviation changes the single-trial false-alarm probability by about 1.9 times (Chapter 40, estimate).

The classification

With this model, three classes of limit can be separated cleanly, following the research dossier for this chapter.

1. Physical or information limits. Photon statistics; data never taken or masked; an orbital arc too short to constrain distance; a planet signal exactly or nearly degenerate with a nuisance, so that $Wh\approx0$. More observations can move these limits. Faster evaluation of the same data cannot.
2. Engineering limits. Detector and calibration stability, data movement, memory capacity, follow-up capacity, software robustness, scheduling. Better algorithms help, but the missing ingredient is often not a new statistic.
3. Algorithmic limits. Avoidable repeated computation, inefficient coverage of the hypothesis space, expensive likelihood evaluation, or a statistically inefficient estimator. A genuine improvement here preserves a stated scientific operating point.

The classes overlap, and the overlaps are where most arguments in the literature go wrong. Stellar activity is a physical source of velocity variability; inadequate activity diagnostics are an observational limit; an overly rigid covariance kernel is a modelling limit. Calling all three “the noise floor” hides which intervention would help. In the same way, a source missed by thresholding single images is not necessarily undetectable in those images. Its signed, subthreshold measurements may still add coherently. The dossier’s own phrase for the test is useful: for any reported speed-up, ask what information, search coverage or statistical guarantee was exchanged for it.

The limits, field by field

The table below compresses the closing sections of the previous forty-one chapters. Each row names the limits that the chapter’s evidence identifies as physical and those it identifies as engineering or algorithmic. Cells are deliberately short; the chapters carry the detail.

What no computer moves

Four physical limits recur through the whole table.

Photon noise. For a stable source in background-limited noise the significance grows as the square root of the collected photons, and the matched filter on the true template is the ceiling. That ceiling is not always reached. In Stetzler and colleagues’ comparison of catalogue and image stacking, the paper’s own reference for an optimal coadd of all 104 exposures at a known position was $m_{50}=26.2$, while KBMOD reached $25.47\pm0.01$ (Stetzler et al. 2025, §4). Part of that 0.7 mag is the unavoidable price of searching many trajectories, which raises the threshold above the five sigma behind the single-epoch reference. The rest is mismatch, filtering and vetting. No published study splits the gap, and splitting it would be one of the most informative small experiments in the field. Exozodiacal dust is the same limit in another costume: subtracting a mean background cannot remove the shot noise of photons already detected (NASA ExEP Science Gap List 2025, SCI-11).

Missing information. A gap in the cadence, a masked chip, a transit that fell in a data gap, an onboard coadd that averaged away the time axis, a voltage phase discarded at detection: none of these is restored by arithmetic. The near-equivalent is a degeneracy. A microlensing light curve constrains $\theta_E^2=\kappa M\pi_{\rm rel}$ and $t_E=\theta_E/\mu_{\rm rel}$, but not mass, distance and motion separately without parallax or astrometry (Chapter 32). An unresolved planet and a persistent speckle with identical modulation cannot be told apart by a better classifier (Chapter 33). Deep PACO’s authors describe a remaining factor of about five to ten between their contrast and a photon-limit reference near the star, and some of that gap may be missing angular diversity rather than a weak algorithm (Flasseur et al. 2023). A sufficiently flexible activity model can absorb a radial-velocity planet, and a restrictive one can invent one (Chapter 29). An Earth analogue moves its star by about 9 cm s⁻¹ (Fischer et al. 2016), and the EPRV working group stated plainly that suppressing stellar variability to the 10 cm s⁻¹ level is not an established capability (Crass et al. 2021). A one-night tracklet barely constrains distance (Chapter 13). Each of these is moved by another observation, not another FLOP.

Confusion. Finite resolution mixes sources. In the thermal and millimetre searches of Chapter 24 the time-varying signal of a body moving less than a beam is its displacement times the beam gradient, and for a parallax-dominated, internally heated planet that falls roughly as $r^{-3}$, not the $r^{-2}$ of its flux. Confusion is partly inferential: better multi-epoch scene models can separate what a static subtraction merges. But the irreducible part sets a floor.

The size of the hypothesis space. The number of distinguishable trajectories, periods or orbits is set by the data: by the PSF, the cadence and the noise. The metric of Chapter 38 measures it, and covering theory bounds how thin a bank can be. A narrower prior reduces it, but changes the population searched. The proper volume is physics. How many redundant passes over the data a search makes in covering it is engineering.

Five losses that keep recurring

The engineering column of the table looks varied, but most of its entries are instances of five losses.

1. Deciding too early. Thresholding single images before combining them, requiring a detection in every night, linking catalogue entries, summing powers, or letting a classifier veto before the evidence is assembled. The measured costs are consistent: about a quarter magnitude for catalogue stacking at a single-image SNR ≥ 2 cut (Stetzler et al. 2025); 0.1–0.2 mag for learned vetting in two surveys (Chapter 22); about 0.2 mag after neural filtering in the New Horizons search (Chapter 6); about 0.88 mag for YOSO’s learned proposals (Pandey et al. 2026); about 0.7 mag for point-source detection applied to a trail six seeing-widths long (Chapter 14). Each can be a sensible operating choice. None is free.

2. Getting the denominator wrong. Interpolation, Fourier shifts, masks and variable seeing distort the information $B$. The project’s benchmark kit measured Fourier null-variance ratios of 1.31 at a mask boundary for a PSF width of 0.55 pixel (Chapter 40). In the radio comparison of Chapter 36, most of the difference between 64.5% and 76.3% simulated recovery came, according to its author, from noise normalisation. The fix is usually known and always costs something, and that cost is what many speed claims leave out.

3. Moving bytes, and Amdahl’s law. If a fraction $f$ of the runtime is accelerated by $s$, the whole speeds up by $[(1-f)+f/s]^{-1}$. In Fink-FAT’s dense test, orbit fitting was 70.83% of the wall time, so even infinitely fast fitting gives at most 3.43 times (Le Montagner et al. 2024; Chapter 15). In Euclid’s streak pipeline, infinitely fast neural inference gives 1.35 times (Pöntinen et al. 2023; Chapter 23). In the LLNL archive search, orbit–image intersection was 44.33 s of a 53.64 s one-node subtotal, and retrieval grew from 9.31 s to 37.37 s as the run scaled to 128 nodes (Golovich et al. 2025). ATLAS’s image path cost ten times its linker, and ZTF hit database limits with CPU to spare (Chapter 14).

4. Redundant hypotheses. Banks laid out on rectangular grids in the wrong coordinates, banks that include impossible trajectories, and exact calculations that cannot change the answer. Lattice shape alone is worth a factor of a few: in six dimensions a hypercubic grid is about 6.8 times thicker than $A_6^*$ at fixed worst-case mismatch, but only 15–20% at fixed average loss (Chapter 38). Bad banks are where larger factors hide, as Parker and Kavelaars’ re-gridding of one published survey from 95 to 28 shift vectors at the same maximum tracking error showed (Parker & Kavelaars 2010).

5. Expensive calibration. Injection–recovery, null resampling and selection functions repeat nearly identical work thousands of times, and their cost often decides how well a search is calibrated. The Kepler-1708 exomoon null test had 200 injections because each photodynamical fit was expensive (Kipping et al. 2022; Chapter 31). A Hubble occultation candidate’s tail calibration cost about 2,300 CPU-days (Schlichting et al. 2012; Chapter 25). Planet Nine selection simulations generated about $10^{10}$ synthetic objects for $10^5$ detections (Chapter 8). This is the loss where GPUs help most easily, and where a faster but wrong answer is most dangerous.

Which large speed-ups were real

The book has collected many reported speed-ups. They are not comparable with one another: each has its own workload, hardware and denominator. But they can be sorted by what they kept, and the sorting carries a clear lesson.

Sources for each row are in the chapters cited, and in Foreman-Mackey et al. 2017, Roa et al. 2021, Shang et al. 2026, Flasseur et al. 2018, Holman et al. 2025, Bernardinelli et al. 2022, Talens et al. 2026, the TLS changelog, Nguyen et al. 2024, Matthews & Nguyen 2026 and Kumar & Zackay 2026.

The pattern is plain. Every gain of a hundredfold or more that kept its statistic came from changing the representation of the problem on the same hardware: structured covariance algebra, sampling the tail instead of the bulk, precomputing maps that many hypotheses share, culling with a conservative bound, replacing a tree query by a two-line membership test. None came from a faster processor running the old algorithm. The gains that came with hardware were real but mixed, as in CETRA’s comparison of an H100 with one CPU core, and one of the largest pure engineering gains in the book, bonsai’s thirtyfold from cache blocking, came on CPUs (CHIME/FRB Collaboration 2018). Some celebrated gains were not speed at all. Transit Least Squares recovered 93.1% of injected Earth-like signals against 75.7% for BLS at the same 1% false-positive rate, because its template was better (Hippke & Heller 2019). THOR’s roughly twofold advantage over an idealised MOPS concerned which objects were findable under the ZTF cadence, not runtime (Moeyens et al. 2021). The large gains on the moving-object problem itself, catalogue stacking, FaXT and YOSO, all changed the operating point: they are faster and somewhat shallower, which is a different and sometimes very useful answer.

A second pattern is that the representation-changing gains have mostly been harvested once already. Fast PACO’s 90 times, celerite’s thousandfold and microlensing’s hundredfold are in the published codes. The next order of magnitude in each of those fields has to be found on top of them, and the chapters are explicit that the first step must not be claimed twice.

The denominator problem

The project behind this book set out, overnight on 15–16 October 2026, to answer a narrow question: is there a credible design space for an order-of-magnitude faster blind faint-mover search on one H100 at equal sensitivity? Its design studies, adversarial reviews and evidence digest are unpublished. Their most useful finding was not a new kernel. It was that the published and modelled factors disagreed mainly because they were measured against different things.

The evidence digest found five different denominators in the project’s own reports: an uncompressed FP32 gather at 2 TB/s, an ideal gather at full bandwidth, a coalesced gather at 60% of peak, a modelled “fastest” INT8 tiled gather at 0.70 trillion pairs per second, and that same model doubled. The modelled INT8 gather was itself never measured. Analogue-field factors quoted against the weakest of these shrank by about four times against an encoded gather; one fell from 10.6 to 2.6 times. Against deployed codes the picture is different again. KBMOD’s published coefficient of $2.4\times10^{-11}$ s per trajectory per image comes from 2019 hardware (Whidden et al. 2019); DEEP’s 576 s per CCD on an A40 includes every pipeline stage; heliostack reports “a few hundred” H200 GPU-hours and a few thousand CPU-hours (Napier et al. 2026). None of these is a same-GPU, same-bank, same-threshold baseline.

The consequence is that one design can honestly be quoted at almost any factor. The lead route of the next section, evaluated on one counted workload, gives the ladder below.

All of these numbers are roofline models. Against a full encoded gather the route looks like 81 times. Give the comparator conditional sequential rejection, as any competent implementation would, and it is 25 times. Give it a design-flux sequential probability ratio test (SPRT) and it is 15 times. Charge the masked-normalisation pass that real data need and it is about 7 times. Under adverse hardware assumptions it is about 3. In the separate LOKI-transfer worksheet, using the table ratio the small image prototype actually measured, the factor against SPRT is about 3, and against an SPRT allowed a 1.4% limiting-flux penalty, 1.8. The top and bottom of this ladder differ by a factor of forty, for the same algorithm.

The general rule follows. Build the denominator first. Every claim in this field should be quoted against a tuned, footprint-aware gather on the same hardware, with the same encoding, the same bank, the same early-rejection rule and the same false-alarm contract, and with stage timings that include I/O. That kernel does not yet exist as a public, measured artefact. Building it is the first item of the programme at the end of this chapter, and it is the cheapest: the project’s estimate is four to eight GPU-hours.

A map of the regimes

The project’s studies found that the answer depends less on the algorithm than on the shape of the data. Two numbers describe that shape: how many useful exposures overlap a typical output trajectory, and how long the arc is. The diagram places the regimes the studies examined.

One night. About a hundred exposures, as in a DEEP CCD of 102 exposures and 1,500 motions. Against a fair baseline the best composite pipeline models at about 1.0–1.6 times. The large numbers here are all engineering: 5.6 to 16.8 times against the historical KBMOD coefficient, and about 190 times against DEEP’s end-to-end 576 s per CCD, which the design study itself labelled “not algorithmic”. The modelled cold common work, 2.09 s, already exceeded the whole 1.80 s tuned baseline search.

A real long stack. Heliostack’s 1,118 Hubble planes look dense, but because the canvas is larger than any one exposure, an average output pixel is covered by only about 51.5 useful epochs. Every dense-epoch operator collapses there: the separable GEMM models at 0.30–1.11 times, the Fourier filter at 0.94–4.35 times. The best composite is about 4.4 times a strong gather, but only 1.5 times a conditional sequential gather and 1.0 times an SPRT gather.

An ideal long stack, with about a thousand exposures each covering the whole output tile. This is the tensor-core regime of Chapter 40 and Chapter 39: the model gives 7.3–24 times against the modelled fast gather, 2.9–9.6 times once a general mask normalisation is charged, and the digest’s best estimate is 2–8 times. Real examples are Rubin deep-drilling fields, HSC and New Horizons sequences, and Hubble or JWST stares with hundreds to thousands of fully overlapping exposures.

Dense multi-night fields, ten to thirty nights of tens to hundreds of visits. This is where the project’s lead route lives, and the next section takes it in detail.

Sparse multi-year archives, a few useful epochs per season over years, as in ZTF or DECam archive searches. The best modelled factors are 2.5–4 times against strong comparators. Geometry and intersection, 83% of the only measured pipeline profile (Golovich et al. 2025), has not been designed for at all. And the absolute scale is sobering. Geringer-Sameth and colleagues forecast about $10^{19}$ orbit trials for a broad multi-year distant-body search (Geringer-Sameth et al. 2025). At a mismatch of $m=1$, which retains only about $e^{-1}$ of the SNR, the project’s estimates for such a search beyond 100 au at ZTF scale run to hundreds of H100-years, in versions from about 450 to 3,000 depending on the assumed bandwidth. A bank with only 2%-class losses would need about a thousand times more trials. No algorithm in the studies makes that a single-GPU job.

Where an order of magnitude may remain

The table ranks the places in the book where a tenfold gain in compute at equal sensitivity is most plausible, by the strength of the case. “Evidence” means the strongest kind of support that exists today. The plausible factors are the chapters’ and the project’s estimates, not results.

The list leaves out places where the chapters agree there is no order of magnitude to find. Radar processing is already regular and transform-based, and is limited by the $R^{-4}$ law and by operations, not arithmetic (Chapter 26). Radial-velocity periodograms and small orbit fits are tiny; their limits are activity, calibration and evidence integration (Chapter 29). Single small least-squares fits do not fill a GPU. And one-night moving-object searches against a fair baseline model at about 1–1.6 times.

1. Engineering against deployed codes

The first entry is the least glamorous and the most certain. The project’s models gave 5.6–16.8 times for an INT8 per-image encoding, footprint-aware tiled gathers and decode-once kernels against the historical KBMOD coefficient. The measurements in Chapter 40 support the direction. The kit’s tiled gather reached 135–145 billion paired samples per second on an A100 at about a thousand epochs, roughly three times the 2019 coefficient on unlike hardware, while still spending its time on double-precision coordinate arithmetic rather than on memory. FP32 coordinates from precomputed offsets, velocity packets staged through shared memory and fused candidate output are known techniques that the chapter estimates at another two to three times on the same card. Against deployed codes, then, a tenfold gain is very likely by engineering alone.

That is worth having. It is also not an algorithmic result, and against a fair same-GPU baseline the same engineering gives only 1.1–2.3 times, because the baseline gets it too. The honest use of this entry is to build the fair baseline, publish it, and quote everything else against it.

2. Dense multi-night fields: the lead route

The idea is old in pieces and new in combination. Over one night of a few hours, a distant body’s track is locally simple, and many distinct long-arc orbits are indistinguishable. So build, for each night, a table of signed $(A,B)$ pairs over a small family of local positions and velocities. Then search orbit cells by combining nightly table entries along each cell’s predicted path, rejecting cells only under a calibrated, permissive rule, and finally recompute every survivor exactly on the original per-exposure maps at the original threshold.

for each night s:
    build signed tables (A_s, B_s) over local position and velocity cells
    (no nightly detection; keep negative evidence)
for each coarse orbit cell, in stages of increasing information fraction:
    gather (A_s, B_s) from the tables along the cell's predicted nightly states
    prune only below a calibrated conditional bound b_s on the final statistic
    refine surviving cells with the subset metric
for each surviving fine template:
    recompute nu = A/sqrt(B) exactly on the original psi, phi maps
    apply the original bank-wide threshold u
calibrate the whole procedure on nulls and injections made before subtraction

Its parts have precedents: KBMOD’s sufficient-statistic maps (Whidden et al. 2019), Parker and Kavelaars’ grid tree (Parker & Kavelaars 2010), the semicoherent hierarchies of continuous-wave searches (Wette et al. 2018), Smith’s pulsar trees (Smith 2016), Geringer-Sameth and colleagues’ metric and their own short-stack proposal (Geringer-Sameth et al. 2025), and above all LOKI’s jointly calibrated multi-stage pruning on GPUs (Kumar & Zackay 2026). What the project added was a reproducible audit of one optical design against strong comparators. Two properties make it safe in principle. Because survivors are rescored exactly on the original fixed bank, selection removes tests and cannot add false alarms to that bank. And a permissive Gaussian gate has explicit dismissal accounting: for a prefix statistic $Y_s$ with variance $f_s$ and covariance $k_s$ with the final score $C$, a source at the threshold $u$ survives the cut

except with probability $\delta_s$, and a union bound over stages controls the total loss without assuming independent stages (Chapter 38, §“A gate that protects faint sources”). With a total dismissal budget of 0.0035 the implied limiting-flux penalty at 90% power is about 0.2%, or 0.002 mag, under the stated covariance and drift conditions.

The number it hinges on. Everything depends on how much nightly table work is needed per unit of fine-bank work it replaces: the ratio $r$ of builder reads to the full gather’s reads. The original cost worksheet needed $r$ below about 0.0098 to reach tenfold against a conditional sequential gather, and below about 0.0015 against SPRT. The small CPU prototypes measured $r=0.0272$ and 0.0744, which the earlier reports had extrapolated pessimistically. The kill test settled this on real geometry.

The kill test used real Subaru Hyper Suprime-Cam exposure records of the New Horizons fields: 980 retained 90-second visits over 92 days in 2020 and 752 over 52 days in 2024 (Yoshida et al. 2024 documents the campaigns). It propagated Keplerian orbits from Subaru’s topocentric position at five seed distances, built a whitened cubic bank at 2% motion mismatch, and counted every quantity exactly by integer enumeration. The central TNO ratios were $1.30\times10^{-9}\le r\le3.73\times10^{-5}$, and the largest across 28 configurations was $1.2\times10^{-4}$, eighty times below the threshold. The reason is physical: a month-long trajectory resolves fine angular rates and curvature, while a four-hour night does not, so one nightly table serves enormous numbers of long-arc hypotheses. The tested bank-cell corners lost at most 1.86% of SNR, below the 2% contract, and in 512 paired raw-pixel draws per case the hierarchy and the exhaustive search recovered exactly the same injected sources. Zero losses in 512 trials gives a one-sided 95% upper bound of 0.58% on dismissal at a fixed flux, not a proof of zero loss.

What it does not show. Substituting the measured $r$ into the unchanged worksheet gave 63.5 times against full gathering, 19.5 against conditional gathering and 11.4 against SPRT. Repricing the actual workloads gave central SPRT factors of 15–23 times, but adverse hardware assumptions gave 3–4. Adding a masked-normalisation pass reduced the most demanding central case to 7.3 times. A 256 × 256 output tile, too small to amortise the common work, gave 1.8. Construction is no longer the problem; gate service, normalisation, bank placement and cold overhead are. The separate LOKI-transfer study measured on CPU, in a 20-night image simulation with curved parallax-like paths and variable PSFs, a 19.2-fold reduction in statistic accesses against exhaustive stacking and 8.6-fold against sequential rejection, with identical blind recoveries in 192 injected cubes. Those are access counts on a CPU, not GPU time, and the same study’s geometry setup (749 ms) dwarfed one warm search (2.6 ms).

The verdict is therefore precise. Dense multi-night fields survive the kill test, and are the most credible place for a tenfold equal-sensitivity gain over the strongest fair H100 baseline. That gain is conditional on a measured GPU implementation of the gate, on charging normalisation under real masks, and on calibration against real subtraction artefacts. None of those has been done.

3. Calibration workloads

The third entry is the easiest to win and the easiest to misuse. Selection calibration repeats nearly identical work: the same detector run on thousands of injected planets, the same statistic on thousands of null realisations, the same survey simulation for many population models. Such work batches perfectly on GPUs. Kepler-1708’s 200 injections could become 20,000 with a hundredfold faster fit (Chapter 31); the Hubble occultation bootstrap’s 2,300 CPU-days is embarrassingly parallel (Chapter 25); the Gaia astrometric wobble search’s roughly $6\times10^8$ simulated noise series can be written as one matrix product per window (Chapter 27). The microlensing chapters estimate the full real-sample degeneracy-aware calculation at about $10^8$ CPU-hours (Chapter 35).

The value of a tenfold here is not depth. It is correctness: thresholds set at a measured rather than assumed false-alarm rate, completeness functions resolved where they change, population inferences that carry their selection uncertainty. Importance sampling and adaptive injection allocation, $n_b\propto|w_b|\sqrt{c_b(1-c_b)}$ in the census chapter’s notation, can add a further factor on top of hardware. The risk is the obvious one: a selection function computed quickly with the wrong noise model, or injected after a preprocessing step that would have removed the planet, is worse than a slow correct one.

4. The second round of exoplanet reuse

The exoplanet chapters each identify a next stage where the first harvest exposed a new bottleneck.

• Transits. On a two-year baseline, CETRA’s periodic stage took about 178 s while its event stage took 0.17 s (Chapter 30; Smith et al. 2025). The periodic stage sums signed numerator and information arrays along combs, which is exactly what fast folding shares across nearby periods (Shahaf et al. 2022). Fast-folding the sufficient statistics, with refinement on the original timestamps, is a natural next algorithm. The comparison must be with CETRA on the same GPU and with TLS 2.0, which has already rewritten the CPU baseline. For active stars the joint transit and correlated-noise model of nuance is the sensitivity reference (Garcia et al. 2024), and in the PLATO stress test its single setup recovered 61.2% of injections against 61.3% for CETRA with four filter windows, at very different cost (Talens et al. 2026).
• Direct imaging. PACOME’s benchmark of $10^9$ orbits over ten epochs took about twenty minutes on twelve cores; the chapter estimates that the same gather would take seconds on one GPU, because the maps total only 168 MB (Chapter 33; Dallant et al. 2023). The saved time is best spent on thousands of null searches.
• Microlensing. Grouping work by lens geometry $(s,q,\rho)$, keeping magnification maps resident and fusing the flux profiling into the same reduction would turn Shang and colleagues’ map reuse into a service (Chapter 32).
• Radial velocity. The useful compute is in exploring several nuisance families and alias modes, not in more samples from one model. Structured kernels already give two to three orders of magnitude (Foreman-Mackey et al. 2017; Delisle et al. 2022), and the Nelson et al. evidence challenge showed that reported internal errors could understate repeatability (Nelson et al. 2018).

Each of these is an estimate. None has an end-to-end benchmark at matched recovery and false-alarm rate on modern accelerators, and the chapters are explicit that Amdahl’s law will cap them at the next stage.

5. Dense long stacks: the tensor-core route

The separable-phase identity of Chapter 40 is the cleanest dense kernel the project found. For straight-line motion plus a known common curve on a Cartesian velocity grid, the velocity plane of the stack at each spatial frequency $\mathbf k$ is one complex matrix product,

with the exposure count as the inner dimension. It is exact (to about $10^{-15}$ in double precision), and FP16 storage of the operands was indistinguishable from exact in CPU emulation. On an A100 the fused kernel reached about 27 TFLOP/s, roughly 9% of FP16 peak, and gave the 5.9 and 1.7 times of this chapter’s opening.

Two facts bound the prize. The route wins by doing more arithmetic on faster units: about 24 useful operations per sample against the gather’s two additions. And it needs density: every exposure must cover every output pixel, or the product multiplies zeros. If the kernel reached the 55% of peak that the Tensor-Core Beamformer reaches on the same card, the scan would fall to about 0.11 s, roughly 4.5 times the ideal no-reuse gather (estimate), and post-processing would dominate. That is a real gain for Rubin deep-drilling fields and long Hubble or JWST stares. It is not an order of magnitude over the best gather one could build, and it does not transfer to sparse or partially overlapping data. The pre-registered acceptance test for an H100, at least 99 TFLOP/s sustained at a thousand exposures with spectra streamed from memory and exact mask normalisation folded in, is still to be run.

6. Upstream density

Because accidental triplets in DES-style linking scale as the cube of the transient density, and false tracks in the Jones model as about its 3.7th power, a modest reduction in false detections at fixed faint-source recall produces a large saving downstream: a factor of $10^{1/3}\approx2.15$ in density gives a nominal tenfold (Chapter 12). This may beat any faster linker. The open question is the price in real faint movers, which must be measured near stars, at chip edges and at the slowest rates, where artefact classifiers are most tempted to reject (Chapter 10).

7 and 8. Sparse archives and learned proposals

For sparse multi-year archives the binding stage is geometry and data movement, not summation. Eliminating retrieval in the one-node LLNL test would gain only about 1.21 times; eliminating intersection would cap that subtotal near 5.8 times (Chapter 20). An indexed, footprint-aware orbit-patch planner that never enumerates impossible orbit–image pairs is the missing design, and nobody has studied it.

Learned proposals have one strong argument: network inference is compute-bound and trajectory gathers are memory-bound, so a small network reading the signed tables a hierarchy builds anyway could decide where exact work is spent (Chapter 22). Every measured case so far carries a depth cost, and the right comparison is with the analytic gates and sequential tests of item 2, which may give most of the gain without training.

The project’s conclusions, and how strong they are

The project that produced this book’s design studies reached four conclusions about moving-object searches on modern GPUs. They are stated here with their evidence level, because the evidence is uneven and the distinctions matter.

Two further findings shaped all four. The first is that prior art defeats broad novelty everywhere. Recursive and tree stacking (FaXT; the grid tree), Fourier velocity filtering (Reed et al. 1983), hierarchical pruning (LOKI, Smith, Weave), metric banks (Geringer-Sameth and colleagues), catalogue stacking (Stetzler and colleagues) and derivative and SVD templates all exist. All eleven of the project’s adversarial reviews returned “partial” or “weak” on novelty. What remains open is narrow and practical: calibrated, economical implementations on real orbit coverage, such as signed-segment pruning for optical orbits under a two-percent contract, and the exact Cartesian velocity GEMM for optical stacks. The second is that every sensitivity result so far comes from Gaussian noise. No study in the project injected sources into real difference images with real artefacts. Real data are less forgiving: the New Horizons Subaru search reported 239 candidates as faint as $r\sim26.5$ without a characterised false-linkage rate (Fraser et al. 2024). Since a 1% error in $\sigma$ shifts a 7.65σ tail by about 1.8 times, this is the largest single gap between these conclusions and a survey.

A research programme

The programme below orders experiments so that the cheapest measurements that could kill the leading ideas come first, and so that every later claim has a denominator. It merges the project’s recommended programme with the benchmark requirements that recur through the book.

The step-1 budget of four to eight GPU-hours is small because the measurement is small: one CCD, a fixed bank, paired injections. It is also the step most likely to change the picture, because every factor in this chapter is quoted against a gather that has never been measured at its best.

Step 3’s kill criterion is deliberately strict. A regime-D prototype that is five times faster than a well-tuned SPRT gather at under 2% SNR loss would already be a significant result. Its failure would be informative too: the project’s models say exactly which stage would be responsible, gate service or normalisation, and the LOKI-style rescue target (reducing combined gate, compaction and normalisation work to about two thirds) is already defined.

The benchmark that would settle the arguments

Most chapters ended by asking for the same missing artefact. Stated once, a benchmark that could establish a genuine tenfold gain specifies, before any winner is compared:

1. the same calibrated inputs, the accessible sky, time and orbit domain, and an explicitly parameterised signal population that includes adversarial cases (curved, fast, slow, near stars, near chip edges);
2. completeness against flux and motion or period, with uncertainty, at a matched global false-detection or false-discovery rate;
3. null samples that keep real subtraction artefacts or stellar activity, and injections made before any stage that could attenuate the signal;
4. candidate-level and final-orbit reliability, including wrong associations and duplicates;
5. complete compute accounting: cold and warm setup, CPU and GPU time, hardware, peak memory, I/O, training and tuning amortisation, and latency;
6. an ablation separating better statistics, narrower coverage, approximation, hardware and engineering from genuine arithmetic reuse;
7. a released implementation with pinned versions, and the injection-derived selection function needed for population inference.

The pieces exist in the papers this book cites. DEEP, the New Horizons HSC fields and heliostack’s public Hubble data release (DOI 10.17909/axjs-nh20) supply moving-object inputs; the Exoplanet Imaging Data Challenge supplies common imaging data but did not measure runtime or tuning cost (Cantalloube et al. 2021), and its second phase found no universal winner for characterisation (Cantalloube et al. 2024); the PLATO comparison of Talens and colleagues is a model of an independent transit benchmark and also shows how easily a duration grid can quietly narrow coverage (Talens et al. 2026). They do not yet fill one table.

Beyond compute

Some of the largest remaining gains in this book are not compute gains at all, and an honest synthesis has to say so.

Observing strategy. Le Verrier turned a survey into a single night by inference (Chapter 3). Choosing a recovery observation by the expected reduction in orbit uncertainty, weighted by the chance of detection, can be worth more than many extra discovery photons (Chapter 13, Chapter 14). Occultation campaigns are geometry problems: in Buie and colleagues’ example, the same chord objective needs about 36 stations for a 100-km body at 2.5 au and about 522 at 43 au, because the ephemeris uncertainty scales with distance (Buie et al. 2025). In coronagraphy, NASA’s roadmap names dark-hole computation and post-processing among the algorithm gaps, and faster estimation inside the control loop changes the data subsequently collected (NASA Coronagraph Technology Roadmap 2024).

Keeping information at acquisition. JWST group differences, retained detector reads and short CMOS frames restore time information that trailing and onboard averaging destroy (Chapter 18, Chapter 23). Here the physical limit itself moves, which no post-processing can do.

Preserving the denominator. A census whose rejected candidates, injection catalogues and pipeline versions are frozen alongside its detections can be reanalysed by every future method; one that keeps only detections cannot (Chapter 35). Napier and colleagues’ characterised-survey test of the extreme TNOs, compatible with a uniform parent distribution, was only possible because survey selection was recorded (Napier et al. 2021). An algorithm that changes which arcs or rates are discoverable changes the population likelihood as well as the discovery count, so selection metadata is part of every search result.

Open methods. The 2017 OF201 discovery linked sparse DECaLS and CFHT detections across years, but its linking method is deferred to future work (Cheng et al. 2025). Public releases of the heliostack and LLNL production codes could not be verified when this book was written. A discovery without a reproducible method leaves its sensitivity unknowable, and every comparison against it unfair to someone.

Where the room is

The physical limits in this book are few and they are the same everywhere: the photons collected, the information never recorded or exactly degenerate with a nuisance, the confusion of finite resolution, and the number of genuinely distinguishable hypotheses. The matched filter on the true template is the ceiling, and in at least one carefully measured case practice sits about 0.7 mag below a simple estimate of it, for reasons nobody has fully apportioned.

The engineering and algorithmic limits are many, and they recur as five losses: deciding before the evidence is assembled, mishandling the denominator, moving bytes that need not move, testing hypotheses that cannot matter, and paying too much for calibration. The large historical gains, a hundredfold or more at fixed sensitivity, all came from changing the representation on the same hardware. Most of those gains are already in the codes.

For moving objects on modern GPUs, the room that remains is narrower than the headlines and better defined than it was. Against deployed codes, a tenfold gain is likely by engineering alone. Against a fair baseline it is conditional, and only in dense data. The best-supported route is dense multi-night stacking with signed nightly tables, calibrated gates, sequential rejection and exact refinement, which survived a kill test on real cadences but has never run on a GPU. The cleanest kernel is the separable tensor-core GEMM, measured once at 5.9 times a kit gather and about 1.7 times an ideal one. For exoplanets, the next factors are in second-round reuse and, above all, in calibration made cheap enough to be done properly.

The first experiment is the smallest one: build and measure the denominator. Until a tuned gather, with the same bank and the same false-alarm rule, has been timed on the same GPU, every speed-up in this field, including this book’s own, is a ratio with an unknown bottom.

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