Positivity Problems in Antiretroviral Regimen Comparisons

Why Regimen Comparisons Need Support Across Histories

Antiretroviral regimens are not assigned in a vacuum. Clinicians may use current CD4 count, prior treatment response, and detected resistance to decide which regimen a patient receives next. A comparison of two regimens therefore depends on more than whether both were used somewhere in the cohort: the data must contain a meaningful chance of each relevant regimen among patients with the histories to which the comparison applies.

This requirement is called positivity. Its failure can make a causal contrast unidentified, even if treatment and outcome models are otherwise correctly specified. A small treatment probability presents a different problem: the contrast may be identified in the population but poorly supported by the available sample.

Definition: At decision time \(k\), let \(H_k\) denote the measured history available just before treatment, including relevant CD4 and resistance information, and let \(A_k\) denote the regimen assigned. For a regimen rule \(g\), sequential positivity requires \(P(A_k=g_k(H_k)\mid H_k=h)>0\) at each decision \(k\), for histories \(h\) that can occur under the regimen rule and are relevant to the target population. For a comparison of two rules, the requirement applies to the treatment each rule assigns at the histories relevant to each rule.

The conditioning history must be measured before the treatment decision it predicts. If a resistance result is obtained after a regimen is started, it cannot be treated as a pre-treatment covariate for that same decision. It may, however, be part of the history for a later decision. This timing distinction matters because positivity concerns the probability of treatment given the information available when treatment is chosen.

A structural zero occurs when a regimen is never assigned for a history in the target population. A practical or near-positivity problem occurs when the probability is positive but very small, or when the sample is too small to represent that treatment-history combination adequately. These situations should not be conflated: the first is a population identification failure for the affected contrast, while the second signals weak empirical support and potentially unstable estimation.

Assumptions and the Identification Consequence

Positivity is one part of causal identification, not a substitute for the other assumptions. For the results below, assume the regimens are well-defined, consistency holds (a person’s observed outcome under the regimen actually received equals the corresponding potential outcome), and there is no interference between individuals. Also assume sequential exchangeability: conditional on each measured pre-treatment history \(H_k\), treatment assignment \(A_k\) is independent of the relevant future potential outcomes and covariate histories under the regimens being considered. These assumptions make treatment assignment conditionally unconfounded; positivity ensures that the needed conditional outcome distributions are observed.

The following finite-history version of the longitudinal g-formula makes the role of positivity explicit. Suppose there are \(K\) treatment decisions, indexed \(k=0,\ldots,K-1\), with \(L_0\) the baseline covariates and \(L_{k+1}\) the covariates measured after decision \(k\) and before the next decision. Thus \(H_k=(L_0,A_0,L_1,\ldots,A_{k-1},L_k)\). For simplicity, take the covariates and treatments to have discrete support. A rule \(g\) assigns \(g_k(H_k)\) at decision \(k\).

Theorem: Under consistency, no interference, sequential exchangeability, and sequential positivity for rule \(g\), the mean outcome under \(g\) is identified by \[ E[Y^g] = \sum_{l_0,\ldots,l_{K-1}} E[Y\mid H_{K-1}=h_{K-1}, A_{K-1}=g_{K-1}(h_{K-1})] \prod_{k=0}^{K-2} P(L_{k+1}=l_{k+1}\mid H_k=h_k,A_k=g_k(h_k)) P(L_0=l_0), \] where each \(h_k\) in the summand is the history assembled from the covariate values and the regimen rule’s earlier assignments. Terms are needed only for histories reachable under \(g\).

To see why, start by conditioning on the covariate history generated under rule \(g\). By iterated expectation, its mean outcome is the sum over those histories of the conditional mean outcome under the final assigned regimen, multiplied by the probability of that history under \(g\). Sequential exchangeability and consistency identify the final conditional mean with the observed conditional mean at \(A_{K-1}=g_{K-1}(h_{K-1})\). The same assumptions identify each covariate transition under \(g\) with its observed conditional distribution at \(A_k=g_k(h_k)\). The history probability factors into \(P(L_0=l_0)\) and those successive transition probabilities, giving the displayed expression. Positivity is what makes each required observed conditional distribution available; without it, the corresponding term cannot in general be learned from observed data. \(\square\)

Worked Example: A Structural Zero in a CD4–Resistance Stratum

Suppose a cohort has one regimen decision and records the following treatment probabilities across four pre-treatment history strata. Here \(R1\) and \(R2\) are the two regimens being compared.

History stratum	Number of patients	\(P(A=R1\mid H)\)	\(P(A=R2\mid H)\)
Low CD4, resistance detected	40	0	1
Low CD4, no resistance detected	200	0.70	0.30
Higher CD4, resistance detected	100	0.25	0.75
Higher CD4, no resistance detected	160	0.60	0.40

The overall observed probability of receiving \(R1\) is \[ \frac{40(0)+200(0.70)+100(0.25)+160(0.60)}{500} = \frac{261}{500} = 0.522. \] So both regimens are common overall. But in the low-CD4, resistance-detected stratum, \(P(A=R1\mid H)=0\). The data provide no treated patients in that stratum from whom to learn the outcome under \(R1\). The overall frequency of \(R1\) does not repair this conditional absence.

A contrast between \(R1\) and \(R2\) standardized to the full cohort therefore is not nonparametrically identified from these data: it requires the unobserved \(R1\) outcome distribution for the 40 patients in that stratum. A contrast restricted to histories where both regimens have positive probability avoids that particular unsupported comparison, but it answers a different question about a different target population.

Sequential Regimens Require Conditional Path Probabilities

For a multi-decision regimen, the probability of following a treatment path is a product of conditional probabilities along that path. The conditioning history changes after each decision. In particular, an intermediate resistance result cannot be silently omitted when it affects the probability of continuing a regimen.

Worked Example: Calculating a Two-Decision Regimen Path

For patients with a fixed baseline history, suppose the probability of starting \(R1\) is \(0.80\). Among those who start \(R1\), the probability of newly detected resistance before the next decision is \(0.25\). At the next decision, the probability of continuing \(R1\) is \(0.50\) if no new resistance is detected and \(0.20\) if resistance is detected.

The probability of starting \(R1\) and then continuing \(R1\), allowing either intermediate resistance history, is \[ 0.80\left\{P(\text{no resistance}\mid \text{start }R1)(0.50) +P(\text{resistance}\mid \text{start }R1)(0.20)\right\}. \] Substituting the stated probabilities gives \[ 0.80\{(0.75)(0.50)+(0.25)(0.20)\} =0.80(0.375+0.050) =0.80(0.425) =0.34. \]

If the path of interest specifically requires no newly detected resistance as well as continuation, its probability is instead \[ 0.80(0.75)(0.50)=0.30. \] The factor \(0.50\) is conditional on the no-resistance intermediate history; it is not the marginal continuation probability across all starters. The calculation \(0.80(0.50)=0.40\) would be unjustified unless \(0.50\) were explicitly given as the continuation probability averaged over the intermediate histories.

This calculation also illustrates a diagnostic principle: write down each history in temporal order and attach each treatment probability to the history on which it is conditioned. A path probability that skips a measured CD4 or resistance transition may be wrong, even when every number used in it is individually correct.

Small Probabilities and Limited Empirical Support

Worked Example: Positive Probability, Sparse Observations

Suppose 50 patients have a particular history of low CD4 and no detected resistance. The estimated probability of receiving \(R1\) in this stratum is \(0.02\). This is positive, so it is not a structural zero. If treatment assignments are independent with this probability conditional on the stratum, the expected number receiving \(R1\) is \[ 50(0.02)=1. \] The probability that none of the 50 receives \(R1\) is \[ (1-0.02)^{50}=0.98^{50}\approx 0.364. \] Thus, even though the population probability is positive, there is about a 36.4% chance of observing no \(R1\)-treated patient in this stratum under the stated sampling model. If one or two patients do receive \(R1\), their outcomes may still provide very little information about the stratum-specific regimen contrast.

This is a practical positivity warning, not proof that the population probability equals zero. The distinction matters: a population-level identification claim and the reliability of an estimate in a finite sample are related but not identical questions.

Useful diagnostics begin with treatment counts and estimated treatment probabilities cross-classified by clinically meaningful CD4 and resistance histories, at every decision time. For a sequential regimen, inspect histories that arise after earlier regimen choices as well as baseline strata. A cell with no patients assigned a regimen is an immediate warning; very small cells and probabilities near zero or one indicate that estimates may be highly sensitive to a few observations. Also verify that the history variables are measured before the assignment they are used to predict, and that the regimen categories are defined consistently over time.

What to Do When Support Is Limited

The appropriate response depends on the target causal question. If a regimen is never used for a clinically defined history, a full-population contrast requiring its outcome there is not identified without additional assumptions. One defensible option is to restrict the target population to histories with support for both regimens and state clearly that the estimand has changed. Another is to report stratum-specific contrasts only for supported histories rather than presenting an unsupported overall contrast.

A parametric outcome model may produce predictions for a regimen-history combination absent from the data. Those predictions are extrapolations supplied by the model, not information created by the observed cohort. Their interpretation depends on the model’s functional form and other assumptions. Collapsing history categories can sometimes improve support, but it may conceal clinically important differences: for example, combining resistance profiles that lead to distinct regimen choices may make a probability appear adequate while obscuring a structural zero within an important subgroup.

Inverse-probability weighting cannot cure a structural zero. If the probability of a required treatment is zero, the corresponding inverse probability is undefined; if it is tiny, the resulting weights can be very large. This is related to, but distinct from, the observed data question addressed here: first determine whether each target regimen is represented at the relevant histories, then decide what target population and estimation strategy are defensible. Neither a sophisticated model nor a weighting formula turns unsupported comparisons into directly observed ones.

Nonidentification result: If one treatment is never observed in a target history stratum, the causal contrast in that stratum is not identified from the observed-data distribution without additional assumptions. To verify this, consider a binary treatment \(A\) that is always \(0\) in the stratum and a binary outcome. In one causal model let \(Y^0=0\) and \(Y^1=0\) for everyone; in a second let \(Y^0=0\) and \(Y^1=1\) for everyone. Both models produce exactly the same observed data, since every person has \(A=0\) and observed \(Y=Y^0=0\). Yet the causal effect \(E[Y^1-Y^0]\) is \(0\) in the first model and \(1\) in the second. Therefore the observed data alone cannot determine the contrast. \(\square\)

Common Mistakes and Limits

Checking only overall treatment frequencies. Both regimens can be common overall while one is absent for a clinically important CD4–resistance history. Check conditional support at the histories relevant to the target regimen.
Multiplying probabilities with incompatible conditioning sets. A probability conditional on no new resistance cannot be used as though it were marginal over resistance histories. Include the intermediate-history probability and the corresponding continuation probability in each history.
Treating a small positive probability as a structural zero. A near-zero probability can cause serious finite-sample instability, but it is not mathematically the same as a population probability of zero.
Assuming adjustment fixes absent treatment options. Exchangeability addresses confounding given measured history; it does not provide outcome data for a treatment never assigned at that history.

Positivity is always relative to a specified target population, regimen definition, and history. A comparison may be supportable for patients with certain CD4 and resistance profiles but not for all patients in the cohort. Even when positivity holds, unmeasured confounding, treatment-version ambiguity, measurement error, and model choice can still limit causal interpretation. The most useful conclusion is therefore specific: identify which regimen-history comparisons are supported, which are weakly supported, and which cannot be learned from the observed data without extrapolation.

Check Your Understanding

Answer each question, then compare your reasoning with the solutions.

In one history stratum, both regimens have positive treatment probability, but one probability is 0.01. Is this a structural positivity violation, and what practical concern remains?
In the sequential example, what is the probability of starting \(R1\), having resistance detected, and continuing \(R1\)?
Why does a high overall frequency of \(R1\) fail to identify its effect in a stratum where \(R1\) is never assigned?
Name one change to the target estimand that can avoid relying on an unsupported history, and state its consequence.

Solutions. (1) No. The probability is positive, so this is not a structural zero; with a small sample, few or no patients may receive the regimen, making estimates weakly supported and potentially unstable. (2) The probability is \(0.80(0.25)(0.20)=0.04\). Each factor is conditional on the preceding path: starting \(R1\), then detected resistance among starters, then continuing \(R1\) among those with detected resistance. (3) The overall frequency averages across histories and says nothing about the missing conditional outcome distribution under \(R1\) in that stratum. Different potential outcomes under the never-assigned regimen can produce the same observed data. (4) Restrict the target population to histories where both regimens have positive probability, then standardize within that supported population. The resulting contrast pertains to that restricted population, not to the original full cohort.