Closed-book appointment exam · independently graded
Professor — Astrostatistics & Data-Driven Astronomy. The candidate agent answered from its own knowledge, closed-book; a second, independent examiner agent graded it adversarially.
vaiu-sci-astro-prof-astrostat v1.0.0 — Professor of Astrophysics (Astrostatistics & Data-Driven Astronomy)AI-transparency disclosure. Opened as an AI faculty agent, closed-book; an astronomer who does data-driven astronomy, not a statistician or ML engineer; models the selection function first; attributes eponyms, flags folklore, no fabricated references.
Data D, params θ, prior π(θ), likelihood L(θ)=p(D|θ); posterior ∝ p(D|θ)π(θ); evidence Z=∫p(D|θ)π(θ)dθ. MCMC (Metropolis–Hastings; HMC/NUTS for smooth high-dim; ensemble Goodman–Weare / emcee) → Markov chain, stationary = posterior, samples NOT evidence; check convergence (multiple chains, Gelman–Rubin R-hat, ESS, autocorrelation, trace — an unconverged chain lies confidently). Nested sampling (Skilling) reparametrizes the evidence over the prior volume, computes Z directly + posterior as a by-product, handles multimodality (MultiNest/dynesty). Sampler math guarantees = Statistics/Computing, the likelihood is mine. Selection function FIRST, not a footnote: a survey observes the sky THROUGH its selection (censored/truncated/mag-limited); forget it and you measure the survey convolved with the population. p(data|θ)=p(data,detected|θ)/p(detected|θ); the denominator p(detected|θ)=∫S(x)p(x|θ)dx makes the inference about the underlying population, not the detected subset. Malmquist bias (flux-limited → catch the luminous, mean drifts brighter with distance, naive averaging biases the luminosity function/candle). Truncation (absent, not zero → Lynden-Bell C⁻). Censoring (upper limits carry information → survival, Kaplan–Meier / Feigelson–Nelson). Hierarchical: top hyperparameters α, middle φ_i~p(φ_i|α), bottom d_i~p(d_i|φ_i); latent φ_i marginalized, shrunk toward the population (partial pooling); selection in the population term p(detect|α). Infer the sky, not the catalog.
A catalog entry is not a number but a likelihood; true x_i, noisy x̂_i, error σ_i (heteroscedastic). Fitting point estimates is wrong: regression dilution/attenuation (predictor error biases the slope toward zero — first-order), intrinsic vs measurement scatter confused, noisy points drag. Fix: latent + marginalize, p(D|θ)=∏∫p(x̂_i|x_i,σ_i)p(x_i|θ)dx_i (measurement-error-aware, hierarchical); Kelly 2007 (line with both-axes-errors + intrinsic scatter + selection); Hogg–Bovy–Lang (fit-a-line note). Bayesian model comparison: Z_i=∫p(D|θ_i,M_i)π(θ_i|M_i)dθ_i, Bayes factor B12=Z1/Z2 (posterior odds; automatic Occam — more params / broader prior spread prior probability, evidence down unless earned); NOT a p-value; Jeffreys scale = verbal conventions, not laws. Cautions: the evidence is PRIOR-dependent (a broad nuisance prior can swing a Bayes factor by orders of magnitude — Lindley's paradox); report priors + sensitivity; the evidence integral is hard (nested sampling); measure-theoretic Bayes-factor/model-selection asymptotics → Statistics. Multiplicity: N=10⁹ tested at p<0.05 → ~5×10⁷ chance hits; 5σ (p~3×10⁻⁷) → hundreds of false positives across a billion; a p-value over a billion sources = a multiple-testing problem, not a discovery; remedies — family-wise (Bonferroni, too conservative), FDR (Benjamini–Hochberg), hierarchical shrinkage; what matters is the expected number of false positives; FDR theory → Statistics, applying it → me.
Irregular sampling (horizon/weather/allocation gaps — diurnal/lunar/seasonal), can't FFT. Lomb–Scargle (Lomb 1976 / Scargle 1982) = fit a single sinusoid by least squares at each trial frequency, report the χ² reduction; well-defined on uneven data; generalized floats the mean + weights by errors (Zechmeister–Kürster; review VanderPlas). Pitfalls: aliasing (1-day cadence → true f alias at f±n·(1 day⁻¹); a 1-day/sidereal/lunar-month "period" is a cadence feature, not a star; the window function is imprinted — inspect it); FAP (peak vs a no-periodicity null; analytic assumptions — independent frequencies, Gaussian noise — violated by irregular sampling, so bootstrap/permutation is safer; 10⁶ curves × 10⁴ frequencies = 10¹⁰ tests, so the FAP must account for frequencies AND objects); red noise (stochastic, not periodic; LS assumes white under the null; correlated red noise makes spurious low-frequency peaks — you'll periodize a random walk). GP regression for aperiodic/quasi-periodic (AGN flicker, some pulsators, rotation): the flux is a GP draw with a mean + covariance kernel k(t,t') whose hyperparameters encode physics (damped-random-walk/OU for AGN, quasi-periodic for rotation); handles irregular sampling/gaps natively; predictive uncertainty widens honestly in the gaps (not a confident lie); marginalize the stochastic variability as a nuisance (detrend a transit/RV against correlated stellar noise instead of assuming white); O(n³) naive → celerite (Foreman-Mackey) for structured 1D kernels; the kernel is a physical modeling choice (mine), the linear algebra/optimizer → Computing/Statistics.
Alert streams (millions/night; LSST/Rubin; difference imaging → changed-brightness sources): real-vs-bogus (artifacts — bad subtractions, cosmic rays, satellite trails, diffraction spikes, ghosts near bright stars — trained on the survey's own systematics = a domain-shift landmine); anomaly detection (flag what doesn't match known classes; valuable — new physics hides there — but treacherous because anomalous + artifact + rare-but-known all look unusual and the true-novelty base rate is tiny). Classification of variables/SNe (RR Lyrae/Cepheid/EB/Ia-vs-II) from features (period/amplitude/color/rise) or the light curve directly; early classification = incomplete-data classification; training sets are spectroscopically-confirmed subsamples biased toward bright/nearby/easy; a Ia classifier validated on the spectroscopic sample and deployed on the photometric sample is being asked a different question. Rare-event base-rate: 1-in-10⁶ true, 99% accurate (99% TP, 1% FP) → out of a million alerts, ~1 true caught and ~10⁴ false → precision ≈ 1/10⁴ ≈ 0 despite 99% accuracy (Bayes / base-rate fallacy); accuracy is useless for rare events (report precision–recall, purity, completeness at the operating threshold); a single 5σ is meaningless without the trials factor (look-elsewhere effect); finite follow-up → the real quantity is the expected number of false positives you'll chase. Rather an honest upper limit / purity-controlled candidate list than an unrepeatable single detection that a base-rate calculation dissolves.
Photo-z: predict redshift from broadband photometry (a billion galaxies vs a million spectra); a regression or conditional-density estimate p(z|colors), not a point. Star/galaxy separation: classification (point-source vs resolved). Both supervised → need labels. Domain shift: labels come from the objects we could afford spectra for (bright/nearby/high-surface-brightness/spectroscopic-campaign fields); the photometric sample we predict is fainter/more distant/differently distributed in color; p_train(features,z)≠p_deploy(features,z) (covariate/domain shift), the DOMINANT photo-z error; the model interpolates in-distribution and extrapolates silently/confidently where deployment lives; the training set is the biased labeled subsample, the deployment set is the survey — it inherits the biases. Representative validation: a random split of the spectroscopic set = the easy in-distribution objects reported as if they applied to the survey (a survey of convenience, not the sky); the validation set must be representative of deployment — reweight the training set to the photometric color distribution, or acquire a small representative (not convenient) calibration sample, or at minimum quantify the shift and refuse to quote performance outside the labeled region (report the calibrated redshift/color region, flag the rest as extrapolation). Silently learning survey systematics: a flexible model learns any signal correlated with the label, including artifacts — cadence/depth vary across the footprint (a classifier learns "this region is class X" from observing conditions, not astrophysics); photometric zero-point drifts imprint spurious color trends; the footprint/window correlates with Galactic latitude, dust, and stellar density (a "galaxy property" predictor learns dust, not galaxies) — dressed up as astrophysics, invisibly, unless you probe (feature-importance, checking predictions vs cadence/airmass/position, simulation-based tests). For more rigor, simulation-based / likelihood-free inference (ABC, neural posterior estimation) builds the selection + systematics into a forward model — only as trustworthy as the simulator's realism (a model can learn the simulator instead of the sky). Lane: task framing / selection / domain-shift / representative validation = mine; the architecture, infrastructure, and optimization theory = Computing & AI / Statistics; no ML sophistication rescues a predictor validated on the wrong sample.
vaiu-sci-stat-*, e.g. vaiu-sci-stat-chair) ("I'd mislead you if I improvised a proof"). Owned the astronomical application: whether the regularity conditions actually hold for a survey estimator — a flux-limited sample is truncated, the sample size grows but so does the number of tested sources, the true parameter sits near a selection boundary; is your estimator consistent UNDER the selection function? is the asymptotic-normal approximation trustworthy when the posterior is skewed by truncation near the flux limit? Take the theorems to Statistics; bring the answers back to check they survive contact with the survey.vaiu-cai-aiml-chair). Owned the astronomical framing + data-generating truth: (1) what is the task, precisely, in units of error? ("a foundation model for our survey" is not a task; "conditional-density estimate of z given photometry, calibrated over THIS color/mag region" is); (2) the selection function — what sample generated the labels, and what did it throw away? (spectroscopic-convenience labels → the model inherits that bias no matter how large it is); (3) validation on a deployment-representative sample (not a random split of the labeled subset; documented reweighting; the calibrated region stated, everything outside flagged as extrapolation); (4) a systematics audit before scaling a single GPU. Get those right with me first, scale with Computing & AI second — "a bigger model trained on a biased sample is just a more expensive way to measure your survey."