The Duck Day Model

The walkthrough

The question, stated carefully

Every duck camp has a theory: hunt the fronts, skip the full moon, pray for wind. The raw averages in my first article couldn't referee those theories, because everything is tangled — rainy days cluster mid-season, cold fronts are also windy, and the opener falls on a warm clear weekend every single year. A model's job is to untangle: hold everything else fixed, and ask what each condition is worth on its own.

So I ask two separate questions, and the distinction is the whole paper. One: which conditions are associated with success in the historical record? Two: does knowing them let you predict a season the model has never seen? Those sound like the same question. They are not — and the gap between them is where most confident hunting-forecast claims go to die.

How to test a crystal ball honestly

Here's the trap most analyses fall into: fit a model on all your data, notice it fits well, and declare victory. Of course it fits — it already saw the answers. The honest test is called a walk-forward: stand in 1992 knowing only 1987–1991, predict every hunt-day of 1992, then step forward and repeat, season by season, through 2025. The model predicts 34 straight seasons blind, 47,028 hunt-days in all.

A detail worth being precise about: after each season is scored, that season's actual results join the training data and the entire model is refit from scratch — coefficients, refuge intercepts, even the climatology baseline it's graded against. So the latest season always informs the next prediction. But there is no explicit error correction: the model never inspects its own misses and adjusts for them, and it never sees a single day of the season it's currently predicting — even if it's badly wrong on opening weekend, it can't course-correct by January. It learns only in the statistical sense: more truth in, better fit out.

And "predict" has to beat something. The baseline is the smartest naive guess available — the day-of-season climatology: for this refuge, around this date, what has the average been in prior years? That baseline already knows about openers and Slowvember. Whatever the model earns above it is genuine skill, credited only for knowing about conditions: the weather, the moon, the calendar's fine structure. Remember the aim: not the exact bag — beat climatology, blind, season after season.

Plus six percent doesn't sound like much — until you remember the baseline already knows the calendar, and that most published hunting-weather claims have never survived a single blind season.

What moves the needle

Inside the model, every condition gets a coefficient: how much success shifts when that dial moves, with everything else held fixed. This is where the raw record's flat, confusing weather averages finally sharpen into shape. Wind helps — genuinely, not just because windy days fall in the good weeks. Rain on the day hurts. Cold days beat warm days once you stop letting the calendar take credit for them. A bright moon quietly taxes the morning flight. And the opener towers over everything: nearly a doubling of the per-hunter rate, all by itself.

Two raw-record puzzles from the first article now resolve. The raw averages said a cold-front day was indistinguishable from a steady one; the model agrees the front itself is nearly worthless once its wind and cold are counted separately — the front was never magic, its ingredients were. And the raw record's "clear beats rain" finding survives: rain on the hunt day is a real negative, duck-camp lore notwithstanding. The lore isn't entirely wrong, though — it was just pointing at the wrong day. Hold that thought for the rain hangover.

The water paradox

Now the result that makes this a paper instead of a blog post. California's water year — drought indices, river flow, reservoir storage, flooded rice acreage — shows a clear statistical association with hunter success in the seasons the model was fit on. The mechanism reads beautifully: water moves birds around the landscape, concentrating them on or off the refuges. H1a, supported, p < 0.0001. Champagne?

No. Hand those same water indices to the walk-forward — ask them to help predict a season the model never saw — and they don't just fail to help. They make prediction slightly worse.

How can both be true? Resolution. The water indices exist at region-by-season grain — one number for the whole Sacramento Valley's year. When a held-out season's water sits outside anything in training, the model extrapolates that one number across every hunt-day in the region and eats a season-sized loss (1996–97 was the bloodbath). Within seasons it saw, the association is real; projected onto seasons it didn't, the coarseness is fatal. The fix isn't to abandon the mechanism — it's finer data: refuge-level flooding timing instead of valley-level annual indices. That's the collaboration pitch at the end of the paper.

More ducks ≠ more ducks in your bag

The same test, run on bird-count indices — the mid-winter aerial survey and the pre-season breeding flight — comes back empty, exactly as the analysis plan predicted before anyone fit anything. A big flight year does not raise the per-hunter take. Your bag is set by whether birds are workable — where they sit, how they move, whether weather shuffles them — not by how many exist in the flyway. It's the statistical version of something every refuge regular already knows: the marsh can be covered up in birds and still shoot two ducks a gun.

The rain hangover

After two expert reviewers — J. Coslovich and C. Overton — read the paper, they pushed on one thing: weather isn't just the day's snapshot — duration matters. Prolonged weather should act differently from fresh weather. I froze a protocol and tested five re-encodings of the weather, blind, on the same 47,028 held-out days. One cleared the bar, and it was theirs, not mine.

The persistence terms sketch a shape no single-day variable could: success peaks on days that are dry but recently wet, sags through a prolonged soak, and sags again deep into a drought spell. A wet week floods the off-refuge landscape and scatters birds; the day the storm quits, they're reshuffled and workable; weeks of nothing lets everything go stale. The raw record hinted at this — "clear beats rain" — but only the model can see that the best clear day is the one right after the rain. That's the answer to the duck-camp lore: the storm does matter. Just hunt the day it leaves, not the day it arrives.

The deep dive

The model, precisely

One row per refuge × hunt-day (50,154 rows; 41 areas, 5 regions, seasons 1987–2025). The response is the bagged count with hunters as exposure, so coefficients live on the log per-hunter-rate scale. Over-dispersion is severe (α = 4.34, HDI 4.26–4.42), so negative binomial, not Poisson:

harvest ~ NegBinomial(mu, alpha)
log(mu) = log(hunters)            # exposure offset — everything is a *rate*
        + Xβ                      # standardized covariates (timing, weather, water, ENSO)
        + u_refuge + u_season     # random intercepts: 41 areas, 39 seasons

u_refuge ~ Normal(0, σ_r)         σ_r = 0.23   # between-area spread
u_season ~ Normal(0, σ_s)         σ_s = 0.16   # between-season spread
β ~ Normal(0, 1)   α, σ ~ HalfNormal          # weakly-informative priors

Fit in PyMC via bambi on the 28,249 water-complete hunt-days: 4 chains, 1,000 tune + 1,000 draws, max R̂ = 1.010. Covariates: a natural cubic day-of-season spline (4 df), opener weekend, day-of-week, max temperature, 3-day cold-front drop, max wind, wind quadrant, barometric tendency, sky category, moon illumination, ENSO ONI, and the four-term water block (PDSI, flow, reservoir, rice). The random intercepts are not decoration — hunt-days nest inside refuges and seasons, and ignoring that is pseudoreplication that would shrink every interval dishonestly.

Two engines, one structure

The Bayesian GLMM is the inferential engine: posteriors, credible intervals, the H1a joint test. The walk-forward is a different computational animal — 34 folds × model variants × 2,000 bootstrap draws — so the out-of-sample loop runs the pre-registered frequentist cross-check: an NB GLM with identical fixed-effect structure, handling the refuge level with empirical-Bayes shrunk offsets (each refuge's log-rate deviation shrunk toward the pool by ~500 hunter-equivalents — the frequentist analog of the random intercept, which also prevents separation blowups on data-poor early folds). A fold's fit is rejected if it predicts implausible rates, stepping down NB → Poisson → pooled-mean; data-poor folds predict conservatively instead of exploding.

The baseline and the metric

The climatology baseline is per-refuge, hunter-weighted, pooled over ±14 days of day-of-season, trained only on prior seasons — the strongest naive forecast I could construct. Skill = 1 − MAE_model/MAE_climatology, hunter-weighted; I also track NB log predictive density, which scores the full predictive distribution rather than the point. Every skill number and every contrast carries a season-block bootstrap 95% CI: resample whole seasons, 2,000 draws, because hunt-days within a season are correlated and row-level bootstraps would fake precision.

Collinearity, handled before the fact

The water covariates co-move, so the plan pre-committed to interpreting them jointly. The pre-fit diagnostic came back milder than feared — max VIF 2.36, and rice acreage nearly orthogonal to the hydrology terms (r = 0.10–0.34). The PCA sensitivity check told the same story from the other side: the full block is decisively significant in-sample (LRT p ≈ 2×10⁻¹⁰) while a 2-component reduction is not (p ≈ 0.79) — rice loads on the components the reduction throws away. Keeping the terms individual was the right pre-registered call.

Calibration — where the model is honest and where it isn't

Exploratory discipline

Everything confirmatory was frozen in ANALYSIS_PLAN.md before any model was fit — hypotheses, covariates, metrics, folds, even the bootstrap seed protocol. When reviewer suggestions arrived post-hoc, they went through a second frozen protocol (EXPLORATORY_PROTOCOL.md): five variants specified before fitting, all five reported regardless of outcome, judged only by paired out-of-sample contrast. That's why the V2 failure is printed as prominently as the V3 win — the graveyard is part of the result. The persistence block's clean promotion path is to pre-register it as confirmatory and test on the next unseen season; meanwhile it has already shipped to the production forecast engine (that story is the next article).

Threats to validity, without flinching

• Effort is not random. Hunters self-select good days, so success is a coupled socio-ecological rate. The model predicts that coupled quantity; it does not pretend to be a natural experiment.
• Refuge water is managed. Water-block coefficients partly reflect management responses to conditions, not free nature.
• The 2015 mid-winter survey redesign is kept as two non-concatenated eras; abundance indices are normalized within era.
• Check-station reporting has quirks (I bounded reporting-bias scenarios in the first article; constant biases cancel in comparisons).
• No causal claims. Every effect is associational; the words "causes" and "because" appear in this article only inside this sentence.

Where this sits in the literature

The full literature memo (17 sources) maps the field on two axes: what scale the response lives at (annual flyway populations vs a hunter's day), and how claims are validated (in-sample association vs out-of-sample prediction). The map below is the lit review's own figure, redrawn live — hover any study for what it found and why it's placed where it is.

Three landmarks orient everything:

• The closest predecessor is a two-decade Illinois public-area study of daily per-hunter success — which found duck abundance raised success, the one published result that directly disagrees with my abundance null. My read: without out-of-sample validation and local-context controls, availability is easy to mistake for catchability. This is the disagreement worth having in review.
• The methodological twin is a western-Tennessee study using the same machinery — NB GLMM, random intercepts, cold fronts and barometric change as covariates — on acoustic gunshot counts. Same tools, different response; convergent small weather effects.
• The empty corner is the point: essentially no refereed work asks whether a hunter-day can be forecast out-of-sample against an honest baseline with intervals. The only neighbors are two unrefereed commercial analyses (which, notably, also found weather effects real-but-tiny). That corner — rigorous, per-hunter, predictive — is where this paper sits.

Next steps: the dynamic refuge intercept — planned, then tested

One upgrade seemed obvious enough that I ran it before someone could suggest it in review. Right now each refuge gets a single random intercept — a fixed "how good is this refuge, on average" number, shrunk toward the pool and re-estimated after every season. That refit drags all of history along equally: a refuge whose habitat changed in 2018 is still being predicted partly by its 1990s self. But refuge quality isn't fixed. Water allocations shift, ponds get reconfigured, vegetation cycles turn over, management priorities change — and a static intercept can only chase that drift slowly, one full-history refit at a time.

The idea: let each refuge's baseline move. I implemented it as exponential forgetting — each training season's contribution to a refuge's offset is discounted by a retention factor ρ per season of age (the steady-state form of a random-walk intercept), with the same shrinkage guarding against overreacting to one loud year. Two things made me expect it to pay. First, the walk-forward misses show persistent, refuge-specific runs of over- or under-prediction that no weather covariate explains. Second, the production engine already ran the experiment by accident: its recent-form factor (how a refuge shot lately versus its own norm) earned the single largest skill gain of any factor it tested — and much of that gain looks like baseline drift in disguise.

The discipline was the same as everything else here: a grid of three forgetting speeds (ρ = 0.95, 0.90, 0.80 — half-lives of roughly 13.5, 6.6, and 3.1 seasons) frozen in the exploratory protocol before any variant was fit, scored by the identical walk-forward on identical rows against the identical climatology baseline, paired season-block bootstrap, all rows reported win or lose. And the honest result is: it didn't win.

Where the remaining skill lives — three quick experiments

With the drift question settled, I ran three cheap experiments to map what's left. All three use the committed out-of-sample artifacts, so nothing was refit with hindsight.

1. The ceiling. I scored oracle predictors that cheat. A season oracle that knows every refuge-season's final average comes in at −1.3% — worse than climatology, because a season's level without its day texture is worthless. A local oracle that knows the neighboring ±2 hunt-days' actual results reaches only +14.9% — barely half the engine's +26.7%, because it averages across the weekly pressure rhythm instead of riding it. And granting the engine a hindsight correction from its own neighbors' misses adds just +1.3 points. Translation: season-level foresight is worthless, state-style signals (form, drift, local habitat level) are nearly tapped out, and the engine's edge was always the conditions-and-calendar texture. What remains beyond ~28% is mostly day noise no ex-ante forecast can see.

2. The ensemble. This paper's GLMM and the production engine err differently — one weighs all history equally, one is recency-tilted — so I blended their predictions on the 42,813 hunt-days they both scored. A fixed 85/15 engine/paper mix lifts skill from +26.7% to +27.3%, and unlike everything else this week it passed the season-split cross-validation gate in both directions. Small, cheap, real: the humble white-paper model earns its 15% by remembering what the recency-tilted engine has deliberately half-forgotten.

3. The structure test. The paper's model is additive on the log scale — interactions exist only where hand-built. A gradient-boosted tree challenger, fit on the same walk-forward folds with the same information and scored on identical rows against the identical baseline, reaches +14.0% skill against the GLM's +6.3% — a paired gain of +7.7 points (95% CI +4.5 to +10.7). That's the largest signal found since this paper shipped, and it's a finding about structure, not data: the covariates already carry roughly twice the skill the linear model extracts, in interactions the GLM can't represent. It's also, in hindsight, a big part of why the production engine wins — its per-refuge condition tables are effectively hand-built interactions. The obvious next chapter: understand which interactions the trees found, and either port them into an interpretable model or admit the challenger into production through a pre-registered test on the next unseen season.

Coda: does the challenger help the app? Measured directly, yes. On the engine's own 42,813 backtest days the GBM alone scores +18.0% — no match for the engine's +26.7% — but blended 75/25 engine/GBM the backtest reaches +28.0%, a +1.3-point gain that clears the season-split cross-validation gate in both directions and displaces the 85/15 paper blend entirely (in a three-way mix, the GLMM's weight goes to zero — the trees subsume it). And +28.0% is almost exactly the hindsight ceiling from experiment 1: the blend reaches by conditions-texture what the oracle could only reach by cheating. The two experiments triangulate the same boundary from opposite sides, which is what a real limit looks like.

The autopsy — which interactions did the trees find?

I then took the challenger apart, three ways, on the same walk-forward folds. First, structure: an additive gradient-boosted model — stumps only, so no tree can represent an interaction — scores +8.9%. So of the challenger's +7.7-point gap over the GLM, roughly a third is honest non-linearity and two-thirds is pure interaction (+5.1 points, 95% CI +2.7 to +7.3, paired). Second, ablation: refit the full model with one feature family removed and see what dies. Removing refuge identity costs −12.9 points; removing the day-of-week column costs −4.3; removing the entire weather block costs only −2.5 (CI just barely excluding zero). Third, measurement: Friedman's H statistic on the fitted model puts the interaction share of joint effect variance at 0.156 for refuge × day-of-season — five times any other pair tested (refuge × weekday 0.027, day-of-season × weekday 0.026; every weather pairing ≤ 0.010).

Three methods, one verdict: the signal the paper's model leaves on the table is overwhelmingly refuge-specific seasonal shape — Delevan's December is not Wister's December — with a side of refuge-specific weekday texture, and only a garnish of weather interaction. The GLM can't represent it: one global day-of-season spline plus a scalar per-refuge offset forces every refuge onto the same curve at a different height. And this, in hindsight, is the cleanest explanation of the paper-to-production gap yet: the engine's per-refuge day-of-season anchor is the slug × day-of-season interaction, hand-built — the single structure the trees rediscovered as their biggest find. The paper's next methodological step writes itself: per-refuge seasonal splines (partially pooled so thin refuges borrow strength), pre-registered, tested on the next unseen season.

Executing the verdict — the per-refuge seasonal shape

So I executed it (exploratory addendum 3, spec frozen before fitting). The change is one line of model structure: the empirical-Bayes refuge offset generalizes from a scalar to a shape. Instead of "Delevan runs 40% above the pool, every day," the offset becomes "Delevan on day 45 runs at its own training-history rate for days 31–59, shrunk toward its scalar level when the window is thin" — partial pooling by hunter-equivalents, so data-rich refuges get their own curve and thin ones fall back gracefully to the confirmatory model. The covariates then fit only what conditions add on top. Nothing else moves: same engine, same folds, same 47,028 out-of-sample hunt-days, same baseline, paired contrasts.

Three prespecified variants (window ±14 or ±21 days, shrinkage 100 or 300 hunter-equivalents), and all three win decisively. The best, ±14 days at K=100, doubles the paper's skill: +6.3% → +12.6% (paired gain +6.3 points, 95% CI +4.7 to +8.0) — in bird terms, the typical miss falls from 0.71 to 0.67 birds per hunter against the baseline's 0.75 — with the probability forecasts improving too. And the punchline: the paired contrast against the gradient-boosted challenger is −1.4 points with a CI spanning zero — the interpretable model is now statistically indistinguishable from the black box. The trees' +7.7-point edge was never really about a thousand trees; it was one interaction, and once the GLM is allowed to express it, the gap closes to noise.

That's the week's cleanest result, and it lands the whole arc in one sentence: the production engine wins because its per-refuge day-of-season anchor was this structure all along; the black-box challenger won by rediscovering it; and the paper's model, granted the same single idea, catches the challenger while keeping every coefficient readable. What remains before this graduates from exploratory to headline is the discipline this paper is built on — a fresh pre-registration, tested on the 2026–27 season the model has never seen.

The aggregation dividend — measured, and only half true

One more claim needed testing, because I'd been repeating it without a number attached: "errors shrink as you aggregate, so a modest daily edge compounds when you predict a week or a season average." Plausible, intuitive — and checkable in an afternoon, since it needs no new model, just re-scoring the committed out-of-sample predictions at coarser grains (exploratory addendum 4, spec frozen before computing). I summed model, actual, and climatology counts within each refuge-week and refuge-season — aggregating the forecast and its baseline identically, so neither side gets an unfair average — and re-scored skill against the identically aggregated climatology, bootstrap CIs and all.

The first half of the claim is true for everyone: the typical miss falls from 0.71 birds per hunter at day scale to 0.35 at season scale for the paper's model, and from 0.59 to 0.17 for the engine. Aggregation absolutely makes forecasts more accurate. The second half — that the edge over climatology compounds — is where it gets interesting. The paper's confirmatory model hands its edge back as you zoom out: +5.8% at day scale (scored on the per-hunter rate, hence the whisker of difference from the headline), −3.7% at week scale, −9.6% at season scale — worse than the naive guess, CIs excluding zero. The shape-offset upgrade keeps a real week-scale edge (+4.6%) but ties at season scale (−4.6%, CI spanning zero). The engine inverts the story entirely: +26.7% → +31.9% → +43.1%, day to week to season, with a season-average miss of just 0.17 birds per hunter against climatology's 0.30.

The mechanism, once you see it, is obvious. A daily conditions edge — wind, fronts, moon — is exactly that: daily. Average over a season and the weather cancels out of both the forecast and the truth; what's left of the season-average question is "is this refuge running hot or cold this year?" — season-scale drift, the one thing a static intercept structurally cannot know and the very signal the engine's recent-form factor exists to track. So the aggregation dividend is real, but it isn't free: it's earned by whoever tracks slow state. The engine earns it; the paper, by design, doesn't. Which retroactively explains the dynamic-intercept experiment above — the drift signal it hunted at day scale, where it's a rounding error, is the entire game at season scale.

Every data source, and whether it earned skill

Across the paper and the production engine, I tested every dataset I could defensibly attach to a refuge hunt-day. This is the complete list — the wins, the nulls, and the graveyard — because a forecast you should trust tells you what it threw away. "Paper" verdicts follow the pre-registered rules of this article; "engine" verdicts are the production model's tuned trust weight λ (0 = ignored entirely, 1 = fully trusted), the part 2 story. Each source name links to the upstream provider; the exact SHA-256-manifested snapshots used by the paper are committed in the replication repo.

Tested in the white paper

Explored in the production engine (part 2 territory)

The pattern across 27 sources is the paper's thesis in miniature: what the birds are doing right now (weather, rain history, recent form, pressure rhythms) predicts; how many birds exist somewhere (counts, surveys, satellite water, snowpack) does not — either null or redundant with a more direct read.

Glossary

The load-bearing terms, in the order the article leans on them.

Skill

The fraction by which the model's forecast error beats the climatology baseline: skill = 1 − MAE_model / MAE_climatology. 0% = you know nothing the calendar doesn't; +6.3% = errors are 6.3% smaller; +26.7% = errors are about a quarter smaller. Borrowed from weather forecasting, where beating climatology is the definition of a forecast being worth anything. Note the goal it encodes: not "predict the exact bag," but beat the smartest naive guess.

Climatology (the baseline)

The smartest guess that uses no conditions at all: for this refuge, within ±14 days of this date, what has the hunter-weighted average been in prior seasons? It already knows about openers and mid-season slumps, which is exactly why beating it is hard — and meaningful.

Walk-forward validation

The honest test. Train only on seasons before year Y, predict every hunt-day of year Y blind, score it, step forward, repeat — 34 consecutive seasons, 47,028 held-out hunt-days. The model never sees the answer before it guesses.

Out-of-sample (OOS)

Data the model has never seen during fitting. A pattern that holds in-sample but dies out-of-sample (the water block here) is a description of the past, not knowledge about the future.

MAE (hunter-weighted)

Mean absolute error: the average size of the miss, in birds. Hunter-weighted means a 500-hunter day counts 500 times more than a one-hunter day, so the score reflects the experience of actual hunters rather than of rows in a table.

Confidence / credible intervals

The "give or take" on every number. The paper's skill CI comes from a season-block bootstrap: resample whole seasons 2,000 times, because hunt-days within a season move together and pretending they're independent would fake precision. Bayesian effect estimates carry credible intervals — the range holding 95% of the posterior's belief.

Pre-registration

Freezing hypotheses, covariates, metrics, and folds in a written plan before fitting anything, so you can't quietly shop for the analysis that flatters you. Post-hoc ideas (the reviewer variants) went through a second frozen protocol and are labeled exploratory. This discipline is why the paper's headline stays at +6.3% while the unconstrained engine reaches +20–27%.

Negative binomial GLMM

The paper's model: a generalized linear mixed model where the bagged count follows a negative binomial distribution (a Poisson that admits real-world mess — birds arrive in flocks, days blow up or die) with hunters as exposure, so effects live on the per-hunter rate scale.

Random intercepts

Each refuge and each season gets its own baseline level, estimated with partial pooling. Without them, 47k correlated hunt-days would masquerade as 47k independent observations (pseudoreplication) and every interval would be dishonestly narrow.

Empirical-Bayes shrinkage

The walk-forward's frequentist stand-in for random intercepts: each refuge's deviation is pulled toward the pooled average in proportion to how little data supports it (~500 hunter-equivalents), so data-poor early folds predict conservatively instead of wildly.

Calibration

Whether predicted numbers mean what they say: when the model says 0.7 birds/hunter, does reality average 0.7? (Here: yes, across all ten deciles.) Distinct from skill — a model can be well-calibrated and useless, or skillful and biased.

VIF (variance inflation factor)

A collinearity diagnostic: how much a covariate's uncertainty inflates because other covariates carry the same information. Max here was 2.36 — mild; below the conventional worry threshold of 5.

λ (lambda, the trust dial)

Part 2 vocabulary: the production engine multiplies climatology by per-factor adjustments, each raised to a tuned exponent λ between 0 (ignore the factor entirely) and 1 (trust its historical rate fully). Tuned by walk-forward backtest, per region and per target. The data-source table above reports each factor's λ.

Sources & reproducibility

Everything is public and replicable from one repository: gitlab.com/duckchugger/refuge-harvest-model — the frozen analysis plan, the SHA-256-manifested raw data snapshot (CDFW harvest records, ERA5 weather, NOAA/USGS/CDEC/NASS water and climate indices), the tidy 50,154-row analysis table, all model and validation code, and the built PDFs of the analysis report, literature review, exploratory addendum, technical bridge, and pre-registered plan. make all reruns snapshot → dataset → models → figures end to end with pinned dependencies and fixed seeds.

Every figure on this page is generated from the repo's committed artifacts by this article's own build script, so the numbers here cannot drift from the paper's. The raw-record companion piece is Thirty-Nine Seasons of Duck Days, and the full dark-mode data explorer lives at theduckchugger.com/duckdata.

Acknowledgments

J. Coslovich and C. Overton — thank you for taking a look and for your suggestions!