Wealth Indices That Survive Attrition

Many studies of poverty and health measure a household's economic position with an asset index. The index is a single score built from a checklist: does the home have a finished floor, piped water, a phone, a motorbike. The usual recipe takes the first principal component of the checklist, which is the weighted sum that captures the most shared variation across items, and treats those weights as fixed facts. In a longitudinal cohort this recipe hides two problems. First, poorer households tend to drop out, so weights fitted on the households that remain describe a richer, narrower sample than the one that enrolled. Second, some checklist items are self-reported, and people over- or under-report them in ways that themselves track wealth. Together these effects can make a cohort look upwardly mobile when it has only lost its poorest members.

We propose to build the index as an explicit statistical model rather than a fixed recipe. Wealth is a hidden quantity measured by noisy items. Self-reported and enumerator-observed items get separate error terms. The model is fitted jointly with a model of who drops out, and Bayesian model averaging is used over the genuinely uncertain choices: which items enter the index, and whether dropout depends only on past wealth or also on current wealth. Bayesian model averaging means combining several candidate models, each weighted by how well it explains the data, instead of committing to one. The averaging is only informative because of one specific ingredient: an area-level deprivation score that is observed for every household, including those that left. It gives the data a way to tell the dropout hypotheses apart. Without it, the averaging would just return the prior.

Core Claim

Our claim concerns longitudinal cohorts in which dropout depends on households' current, unobserved economic state. In that setting, an attrition-aware latent wealth index should give less biased and better-calibrated estimates of wealth mobility and its downstream health associations than the standard pipelines. The standard pipelines are a principal-component index on survivors, or multiple imputation or inverse-probability weighting followed by a principal-component index. This should hold when an auxiliary measure observed for dropouts is available.

We also make a negative claim and intend to test it. When dropout depends only on observed history, the proposed model should match the simpler pipelines and not beat them. When no auxiliary measure exists, the posterior weights over dropout mechanisms should stay near their prior, which shows the averaging adds honesty about uncertainty but not information.

Where This Sits

The motivating evidence comes from three groups of papers.

The first group shows the composite index is the right object but is fragile. Studies show that income alone misses structural deprivation such as housing materials and water access (Poverty Level Characterization via Feature Selection and Machine Learning; Socioeconomic status, depressive symptoms and cardiometabolic kidney syndrome). Asset-based principal-component indices are therefore the working standard, used to track life-course wealth mobility in a rural Chinese birth cohort (Associations between life-course household wealth mobility and adolescent physical growth...) and to harmonize economic position across 18 sub-Saharan surveys (Ethnicity and anthropometric deficits in children). Both treat the loadings, meaning the item weights, as fixed. We instead treat them as uncertain and estimate them jointly with dropout.

The second group bears on how composites are built. Composite variable bias: causal analysis of weight outcomes shows that building composites without proper conditioning on baseline biases longitudinal causal estimates. It motivates estimating mobility inside one model rather than differencing two separately built indices.

The third group shows dropout and self-report interact with economic position. In a large digital-therapy cohort, cost was the most cited cancellation reason (38.77%). That study also had to drop sociodemographic factors because of missingness (Gender Differences in Trajectories of Depressive Symptoms Among Talkspace Clients). Self-reported economic items are known to carry social-desirability and recall error, which then flows into any index built from them.

The averaging machinery comes from prior work. Model averaging improved prediction-interval coverage in small survival subgroups, where no single model dominated (Modelling survival data to account for model uncertainty). That work treated dropout as ordinary censoring. We treat dropout as informative and make the dropout mechanism itself one of the things averaged over. Two other papers constrain the design.

not-MIWAE models missingness that depends on unobserved values. It also stresses that such mechanisms are not identifiable from observed data alone. This is why we refuse to average over dropout models without an auxiliary measure observed for dropouts: the marginal likelihoods would differ only through untestable functional-form choices.

Dangers of Bayesian Model Averaging under Covariate Shift shows full model averaging can underperform a single best-fit (maximum a posteriori, MAP) estimate by up to 25% under distribution shift. The cause is that the prior injects noise along directions the training data never constrained. Attrition creates exactly such a shift. Survivors rarely lack the assets that distinguish the poorest households, so loadings on those items are weakly constrained. We take that warning seriously in two ways. We use a data-dependent prior on loadings, centered on the enrollment-wave covariance, in the spirit of that paper's empirical-covariance prior. We also include MAP as a baseline that may win.

Research Program

The model has three linked parts.

The measurement part. It relates each household's latent wealth at each wave to binary and ordinal asset items through item-response style links. Enumerator-observed items, such as floor and wall materials, have one error structure. Self-reported items, such as durable goods and income bracket, have an additional bias term allowed to vary with latent wealth. This is how social desirability enters.

The dynamics part. Latent wealth evolves across waves.

The dropout part. The probability of leaving at each wave depends on past observed wealth under a missing-at-random hypothesis, or also on current latent wealth under the missing-not-at-random hypotheses. The latter come in two directions: a fragile-poor exit, and a healthy or prosperous exit, such as migration for work.

A census-linked area deprivation score enters as a second, coarse measurement of latent wealth. It is available for every household at every wave. Because this score is observed after dropout, it carries information about the current wealth of those who left, and this is what separates the dropout hypotheses.

Averaging happens over a modest discrete space: a few theory-driven item subsets crossed with the three dropout hypotheses. Marginal likelihoods will be computed by bridge sampling for small spaces, and checked against the BIC approximation used in the survival work above.

The downstream quantity of interest is a model-averaged posterior for a wealth-mobility effect on an outcome, such as adolescent height-for-age. Following CBMA, we will also report a conformal check on the predictive side. That paper gives finite-sample coverage under exchangeability. Attrition breaks exchangeability, so we will report the conformal result only on the enrollment-wave subsample where exchangeability is plausible, and say so.

Baselines

Naive index on survivors. The naive reference point is the standard practice: compute a principal-component asset index separately at each wave on the households present, then regress the outcome on index change. It uses the same items and the same households as every other method. Beating it means lower absolute bias in the mobility effect and nominal 95% interval coverage where it falls short.

Multiple imputation or weighting. The strongest existing pipeline handles attrition first and builds the index second. In one variant, chained-equation multiple imputation under missing-at-random fills in dropouts' items. In the other, inverse-probability-of-attrition weights are fitted from baseline and past-wave covariates, including the area score. A fixed principal-component index is then built in both variants. This is the strongest competitor because it already uses the auxiliary area score and is what an applied epidemiologist would do. To keep the comparison fair, it receives the same covariates, the same area score, and the same tuning budget for the imputation and weight models. Beating it requires a bias reduction outside Monte Carlo error under missing-not-at-random simulations, without losing to it under missing-at-random simulations.

MAP version of our model. The MAP version fits the joint model by selecting the single highest-evidence model and plugging in point estimates. Given the covariate-shift result, it is a real threat. It tests whether averaging, rather than the joint model structure, earns its place.

Ablations. Three ablations isolate the key ingredients: removing the area auxiliary score, collapsing self-reported and observed items into one error structure, and fixing loadings at enrollment-wave values.

No reported result was found on Lacuna for asset-index bias or coverage under cohort attrition. The only reported calibration reference is the survival study's 94% model-averaged interval coverage against 90% and 92% for single models, which we use as context rather than as a target.

Why not just…?

Why not just impute missing waves and then compute the usual index? If dropout depends only on observed history and the area score, imputation under missing-at-random is consistent, and we expect it to tie with our method. The experiment includes exactly that scenario as a no-harm check. Imputation cannot correct dropout driven by current unobserved wealth unless the area score fully explains it. Whether that partial explanation leaves meaningful bias is an empirical question, settled by the missing-not-at-random simulation arms. If imputation matches us there too, the proposal reduces to "always link an area score into the imputation model." That is a useful finding, and we would report it as the main result.

Why not just pick the best single model by BIC instead of averaging? The survival study shows single-model dominance can disappear in small subgroups, which is our regime among the poorest survivors. The covariate-shift study shows averaging can be worse than a point estimate when unconstrained directions are activated. The MAP baseline and the prior-choice ablation measure which effect wins here. We commit to reporting MAP if it is better.

Why not just use income instead of an asset index? Income misses structural deprivation, per the poverty-characterization and cardiometabolic studies cited above. Income is also the most self-report-contaminated and most often missing item, which is precisely why the Talkspace analysis could not adjust for socioeconomic status. Income stays in the model as one self-reported indicator, and a baseline replacing the index with income alone is reported.

Why not just run a tipping-point sensitivity analysis? A delta-adjusted analysis shifts imputed values by a chosen amount and reports where conclusions flip. It is the honest default, and we include it. It reports a curve, not a weighted answer. Our method is only better if the area auxiliary measure actually moves the posterior weights. That is checked directly below.

Proposed Experiments and Decisive Checks

Semi-synthetic test bed. Ground truth is unavailable in real cohorts, so the main evaluation is semi-synthetic. We take complete household asset modules from the sub-Saharan Demographic and Health Surveys (Ethnicity and anthropometric deficits in children), fit a latent wealth model, and simulate four-wave panels from it with known mobility effects on a simulated growth outcome. We then impose three kinds of dropout: missing-at-random given history, fragile-poor exits that depend on current wealth, and prosperous exits. Each is run at three strengths. Separately, we inject wealth-dependent misreporting into a designated set of self-reported items.

Metrics. We measure bias and 95% interval coverage of the mobility effect, Spearman correlation between estimated and true household wealth, and the rate of misclassification into wealth quintiles.

Real-data application. The western China birth cohort (Associations between life-course household wealth mobility...) is the real-data target if access is obtained. There we report how much the published mobility associations move under the averaged model. We will not claim correctness on real data, only sensitivity.

Decisive checks. Three results would settle the proposal.

The first is the no-harm check. Under missing-at-random dropout, our method's bias should be statistically indistinguishable from the imputation-plus-index baseline. If it is clearly worse, the joint model is misspecified and the project stops there.

The second is the identifiability check. With the area score removed, posterior weights over dropout hypotheses should remain close to their prior across simulation arms. With the area score present, the weights should concentrate on the true mechanism as dropout strength grows. If weights concentrate even without the auxiliary measure, the averaging is reading functional-form artifacts and cannot be trusted.

The third is the measurement-error check. Under injected wealth-dependent misreporting, the split error structure should reduce quintile misclassification among the poorest households compared with the pooled ablation. This is where the self-report component either justifies itself or is dropped.