House-price models routinely put a dollar value on things most houses do not have nearby: a clinic within walking distance, a river that floods to five meters, a large-lot zoning allowance. In the data, such an amenity is zero for the large majority of properties and positive, often with a long tail, for the rest. This note proposes to test a simple, checkable suspicion. The price attached to the intensity of a sparse amenity is learned almost entirely from the minority of properties where it is nonzero. If so, it should be overturned by deleting a far smaller fraction of sales than the price attached to a dense attribute like floor area. We also propose that most of this fragility comes from a modeling error. Standard models treat every zero as a valid comparison case, including properties where the amenity could never exist.
The proposal has two parts. The first is a measurement study. Using provable audits of how much data must be removed to flip a coefficient's sign, it compares the stability of sparse-amenity prices with that of dense-attribute prices on public and large-scale housing data. The second is an estimator. It models each sparse amenity with a zero-inflated count model, which separates "structurally impossible here" zeros from "possible but absent" zeros. It then estimates the amenity's price effect only among properties where the amenity was possible, using a rank-based dependence estimate that limits how much any single sale can move the answer. The claim is concrete. This combination should raise the fraction of sales that must be deleted to overturn the conclusion, without costing price-prediction accuracy, and without simply reproducing what a count of nonzero properties would already predict.
Background and what is actually open
Hedonic pricing models split a heterogeneous good's price into implicit prices for its attributes, typically by regressing log price on attributes. The two most relevant recent analyses both handle sparse attributes in ad hoc ways. Examining Property Value Increment along Greenways uses distance buffers on 106,328 Chengdu resales and finds the largest gain, 365.23 CNY/m², in the 500m–1km band. The relationship of single-family detached house prices with neighborhood walkability and disaster risk runs quantile regression on 71,289 Tokyo sales with 16 facility densities and flood-depth hazard bands, and reports elasticities of −0.278 at the 85th price quantile versus −0.113 lower down for >5m flood zones. Neither asks how many sales those numbers rest on. These papers motivate the work: they are exactly the kind of policy-relevant sparse-amenity estimates whose stability is unknown.
The tool that makes stability measurable is Provably Auditing Ordinary Least Squares in Low Dimensions. It gives polynomial-time algorithms that bound the smallest fraction of samples whose removal flips an OLS coefficient's sign. On Boston Housing it found cases where greedy removal by individual influence declared a result stable, yet dropping 8% of the data nullified it. It also certified bounds within a factor of two for most feature pairs. This paper both supplies our measurement method and constrains our design. Its certificates exist only for OLS in roughly three or four dimensions, so any claim about non-OLS estimators must rest on attack-based upper bounds rather than certificates. We say so explicitly below.
Zero-inflated negative binomial (ZINB) models represent a count as a mixture. A gate with probability $\pi$ produces a "structural" zero, and otherwise a negative binomial with mean $\mu$ and dispersion $\theta$ produces the count, which can itself be zero by chance. In the file this machinery appears only in single-cell genomics decoders (ZINB-Based Graph Embedding Autoencoder for Single-Cell RNA-Seq Interpretations) and related settings, and always as a model of the outcome. We use it differently, as a model of a covariate whose gate tells us which properties are legitimate comparisons. The known identifiability problem, where structural and sampling zeros blur when gating and count covariates overlap, is a real constraint. We therefore require gating covariates, such as zoning class, land-use designation, and hazard-map coverage, that plausibly affect feasibility but not intensity.
Rank correlation measures monotone association from orderings alone, so one extreme sale moves it by at most one rank position. latentcor: Fast Computation of Latent Correlations for Mixed Data and its companion latentcor: An R Package for Estimating Latent Correlations from Mixed Data Types supply the method we reuse. They compute Kendall's $\tau$ (pairwise concordance) and invert a bridge function to recover a latent Gaussian correlation for continuous, binary, and zero-truncated variables. In a synthetic check they recover 0.4766 for a true value of 0.50, where Pearson gives 0.4224. latentcor has been used only for exploratory correlation matrices, never as the engine of a regression whose coefficients carry prices.
Core Claim
Sparse-amenity coefficients in hedonic regressions are much less stable under small-fraction data deletion than dense-attribute coefficients. A large part of this instability is excess leverage from structural-zero properties that are not valid counterfactuals. Restricting or weighting the intensity comparison by the ZINB posterior probability that a property is "at risk" of having the amenity removes that leverage. Estimating the conditional effect through a truncated-variable Kendall-$\tau$ bridge then bounds the influence of the remaining tail. The new contribution is the use of a covariate-side zero-inflation gate as a comparison-set definition, joined to a rank-based coefficient, and evaluated by deletion stability rather than fit.
Research Program
The first component is the audit. For each target amenity coefficient, we fit the usual specification: log price on controls, a presence dummy, and log(1+count). We then partial out the controls (the Frisch–Waugh–Lovell step), which leaves a two- or three-dimensional problem: the dummy, the intensity, and an intercept. On this reduced problem the Moitra–Rohatgi algorithms give certified lower and upper bounds on the sign-flip removal fraction. Partialling on full data is an approximation, because deletion also changes the residualization. So every removal set the audit finds is refit in the full specification to confirm that the flip actually occurs. The audit is run on dense attributes in the same regressions, which gives a within-dataset reference.
The second component is the estimator. For a sparse amenity $A_i$ at property $i$, we fit a ZINB with gate covariates $z_i$ (zoning, land use, hazard-map coverage) and count covariates $w_i$. We then compute each property's posterior probability of being at risk, $r_i = 1 - P(\text{structural zero} \mid A_i, z_i, w_i)$; this equals 1 for any property with $A_i>0$. The price effect of intensity is estimated only from properties with high $r_i$, either by a threshold or by weighting with $r_i$. Within that set we compute the Kendall-$\tau$ latent correlation matrix among residualized log price, the amenity, and key controls, using latentcor's truncated bridge. The amenity's latent regression coefficient follows from that matrix. Cardinal prices are needed for policy, and rank methods discard magnitudes. We therefore map the latent effect back to CNY, yen, or dollars by simulating price changes through the fitted Gaussian copula with empirical marginals. A bootstrap supplies uncertainty. The cost of the latent-Gaussian assumption is real. We test it with a copula goodness-of-fit check and report where it fails rather than hide it.
The third component is a semi-synthetic testbed. It keeps the real covariates, including the real zero patterns, and simulates prices with a known shadow price for one sparse amenity. Two contaminations are planted: a coordinated cluster of nonzero-amenity sales with shifted prices, the "joint influence" case that greedy methods miss, and heavy-tailed noise. Because the truth is known, both bias and stability can be scored.
Baselines
The do-nothing reference is the specification practitioners actually run. It is OLS with a presence dummy and log(1+count), with standard errors clustered by neighborhood, fitted on the same sample and controls as every other method. Its audited removal fraction is the number to beat. In semi-synthetic runs its bias is the reference bias.
The data-cleaning reference is the same OLS after removing the top 1% and 5% of sales by Cook's distance. The question is whether greedy cleaning already delivers the stability gain. Moitra and Rohatgi report that on Boston Housing the greedy heuristic declared some regressions stable when an 8% removal overturned them. That figure (8% removal sufficing to nullify a result the greedy method called stable, Provably Auditing Ordinary Least Squares in Low Dimensions) is the strongest reported number on the exact stability question. Our Boston replication must reproduce it before we trust anything else.
The strongest robust-estimation competitor is a Huber or least-absolute-deviation M-estimator, along with quantile regression at the 15th, 50th, and 85th percentiles as in the Tokyo study. Quantile regression is the method that produced the −0.278 versus −0.113 flood elasticities on Tokyo (The relationship of single-family detached house prices with neighborhood walkability and disaster risk). Neither the Tokyo nor the Chengdu study reports a deletion-stability figure, and no reported result was found on Lacuna for removal-fraction stability on either dataset. Our own runs of these baselines therefore set that bar.
Two ablations isolate the key ingredients. Rank-only applies the Kendall bridge to all properties, ignoring the ZINB gate. Gate-only uses at-risk restriction with ordinary OLS. If gate-only matches the full method, the rank component is unnecessary. If rank-only matches it, the ZINB component is unnecessary.
Fairness is enforced in four ways. All methods use identical samples, controls, and fold splits. Tuning budgets are matched: Huber's threshold, the quantile grid, the ZINB gate threshold, and the bridge grid each receive the same small cross-validated search. Stability is scored for every estimator by one shared attack suite: greedy influence removal, approximate-influence ranking, and the removal sets found by the OLS certificate, transferred across estimators. This gives comparable upper bounds, and only OLS-family methods additionally receive certified lower bounds. Beating the baselines means two things together. First, a higher attack-based removal fraction than both Huber and cleaned OLS, consistently across amenities, with semi-synthetic bias no worse. Second, out-of-sample price prediction within noise of the OLS reference.
Why not just…?
Why not just use the presence dummy plus log(1+count) and cluster the standard errors? This is the do-nothing baseline. Clustered standard errors describe sampling variability under the model. They say nothing about whether a small coordinated subset drives the sign, and the Boston audit shows that conventional diagnostics can call a result stable when 8% of the data overturns it. If the dummy specification turns out to be as stable as the proposed estimator on sparse amenities, the core claim is false and we will report that.
Why not just use Huber regression or quantile regression? This is the most serious threat. These estimators bound the influence of large residuals. The failure mode we hypothesize, however, is leverage: structural-zero properties that pile up at the zero boundary and define the intensity slope. Sub-quadratic losses do not reduce that, a limitation noted for M-estimators in A General Framework for Fair and Robust Regression's setting. Quantile regression also degenerates at low quantiles under excess zeros. Still, this is an empirical question. The gate-only ablation run with a Huber loss will show whether gating plus an off-the-shelf robust loss already captures the gain. If it does, we will recommend that simpler combination and drop the rank bridge.
Why not just report how many properties have a nonzero amenity? This could make the whole project a one-line rule. If the removal fraction for a coefficient is predicted almost perfectly by its nonzero share, practitioners need only that count. We test this directly by regressing audited removal fractions on nonzero share across all amenity–dataset pairs. The question is whether ZINB-estimated structural-zero mass and tail heaviness explain stability beyond nonzero share. If they add nothing, we will say so and state the finding as the rule.
Why not just model the outcome with a Tweedie or ZINB likelihood? Price is not zero-inflated. The sparsity lives in the covariates, so outcome-side mixtures, such as those in Deep Extreme Transformer, address the wrong variable.
Proposed Experiments
Boston Housing is the calibration set. It is public and the Moitra–Rohatgi audit has already been run on it. It also contains a classic zero-inflated covariate, the large-lot zoning share, which is zero for most tracts, alongside the river dummy and heavy-tailed crime rate. We first reproduce the reported factor-of-two certification and the 8% greedy failure. We then compare the removal fraction for the zoning coefficient with that for dense covariates, under OLS, the baselines, and the proposed estimator. The low dimension of Boston lets us give certified bounds for nearly every specification there.
The main tests use the Chengdu greenway resales and the Tokyo detached-house sales. Chengdu provides 106,328 sales with POI counts, many of them sparse at fine radii. Tokyo provides 71,289 sales with 16 facility densities and flood-depth bands that are zero for most homes. Access to the Tokyo listing data is a real risk because it comes from a commercial provider. If it is unavailable, we fall back to Chengdu and Boston and say so. In each dataset we audit every sparse amenity and a matched set of dense attributes. We also re-estimate the published headline numbers, the 365.23 CNY/m² greenway band and the flood elasticities, to report how many sales each one rests on. That number is itself a contribution, independent of whether our estimator wins.
Three outcomes are decisive. First, sparse-amenity removal fractions should be systematically lower than dense-attribute fractions in all three datasets; if not, the motivation fails. Second, the full estimator should raise sparse-amenity removal fractions over Huber and cleaned OLS under the shared attack suite, with no loss in held-out log-price error, and the two ablations should each fall short of it. Third, in the semi-synthetic testbed with a planted coordinated cluster, the full estimator should recover the planted shadow price with lower bias than all baselines. Its advantage should shrink when the cluster is moved into structural-zero properties, which confirms that the gate, not luck, does the work. Finally, the nonzero-share regression decides whether the publishable result is a new estimator or a simple reporting rule. We will commit to whichever the data supports.
References
- Examining Property Value Increment along Greenways: A Hedonic Pricing Analysis in Chengdu, China
- The relationship of single-family detached house prices with neighborhood walkability and disaster risk
- Provably Auditing Ordinary Least Squares in Low Dimensions
- ZINB-Based Graph Embedding Autoencoder for Single-Cell RNA-Seq Interpretations
- latentcor: Fast Computation of Latent Correlations for Mixed Data
- latentcor: An R Package for estimating latent correlations from mixed data types
- A General Framework for Fair and Robust Regression
- Deep Extreme Transformer: Tackling Zero-Inflated Time Series for Precipitation Prediction