Marginal Structural Models, G-Computation, and G-Estimation

918 HIV-infected US men and women, followed a median of 5.8 years between 1996 and 2005. Nobody was randomised. The people who kept taking the drug were not like the people who stopped. So each person was reweighted by how surprising their own sequence of decisions looked — surprising given what had been recorded about them at the time each decision was made. Cole and Hernán published that analysis in 2008, with the numbers attached.

The untruncated stabilised weights had a mean of 1.04 and a standard deviation of 1.15. Their maximum was 46.8.

That is the whole lesson in three numbers. The typical person in that analysis counted about once. Somebody in it counted 46.8 times. The weighting model considered the history they had actually lived very unlikely, and the inverse of a small probability is a large number. The model fits cleanly either way. Nothing in its output complains. What the output does not say is that the final estimate is substantially the story of the few people at the top of that distribution. The analysis has built a pseudo-population: a reweighted copy of the data in which treatment no longer depends on the past. The copy can be perfectly well behaved and nearly empty of information.

Four terms do the work for the rest of this lesson. The case above is easier to read once they are separate.

The usual checks are computed one decision at a time. Is the treated group comparable to the untreated group at this moment? Does everyone here have some chance of either assignment? Every one of those checks can come back clean while the product of them falls apart. Probabilities multiply. Comparisons do not.

Treating that as a real problem rather than a box to tick has a protocol behind it. Petersen and colleagues wrote it in 2012, and their statement of the problem is flat and worth having in front of you: “Positivity violations occur when certain subgroups in a sample rarely or never receive some treatments of interest. The resulting sparsity in the data may increase bias with or without an increase in variance and can threaten valid inference.”

Note what that sentence does not say. It does not say the data violate positivity, full stop. Positivity is set out there as a model- and parameter-specific identifiability problem — a property of the estimator and the question, not a defect the dataset carries around on its own. The paper proposes the parametric bootstrap as a diagnostic for how badly sparsity is biasing a given estimator. It then catalogues four responses. Each of the four buys identifiability by moving away from the question you started with. The honest version of the work is to say which move you made.

The trap is worth stating plainly, because all three methods exist because of it. In a study that follows people over time, one variable can be both a consequence of earlier treatment and a cause of the next treatment decision. Adjust for it the ordinary way and you erase the part of the effect that travelled through it. Leave it out and it confounds every later decision. Ordinary regression has no setting for a variable that is both.

Zidovudine and survival in the Multicenter AIDS Cohort Study showed what that costs. The founding applied paper on marginal structural models ran that analysis in Epidemiology in 2000. CD4 count sits in exactly the double role: a confounder of the next treatment decision, and a consequence of past treatment. The crude mortality rate ratio was 3.6 (3.0–4.3). Adjustment for baseline covariates by standard methods brought it to 2.3 (1.9–2.8) — still, read at face value, a drug that kills the people who take it. Then the abstract: “Using a marginal structural Cox model to control further for time-dependent confounding due to CD4 count and other time-dependent covariates, the mortality rate ratio was 0.7 (95% conservative confidence interval = 0.6-1.0).” One dataset, one exposure, three numbers: 3.6, then 2.3, then 0.7. The estimate crosses from strong harm to apparent benefit purely by changing how the sequence of decisions is handled.

Marginal structural models take the first route out. They leave the confounding out of the model and push it into the weights, reweighting the observed histories until treatment no longer depends on the past — the pseudo-population from the case.

The parametric g-formula takes the second. Rather than reweighting anyone, it models the whole longitudinal process: how covariates move, how outcomes follow. Then it simulates that process forward under an intervention you name.

Structural nested models take the third. They parameterise the blip: the small change in outcome from a bit more treatment at one moment, given everything that came before. G-estimation then finds those parameters through treatment residuals.

Picture travellers moving through a sequence of junctions, where the sign at each junction was reset by whoever came through earlier. You can reweight the travellers you actually observed until the signs stop mattering. Or you can model the signs and send simulated travellers through instead. Either way, a rare complete journey may rest on very few people. Junctions at least stand still. A patient's choices can also turn on how they felt that week. Nobody wrote that down, and no amount of reweighting or simulation recovers what was never recorded.

What all three share is the price of admission. At every decision point, the recorded history has to be enough to make treatment as good as random. And the histories you want to compare have to be histories somebody actually lived.

Most of this is decided before there is code. Say first what strategy you are actually asking about: stay on therapy throughout, stop at a threshold, follow a rule that responds to the patient's state. Then decide how history will be represented. That means choosing what counts as the past at each decision point, and what gets carried forward. Only then choose the g-method. That choice depends on which parts of the system you can model credibly, and you do not know that until the first two questions are answered.

This ordering is not one author's preferred habit. It is written into an adopted international guideline. ICH E9(R1), the harmonised addendum on estimands and sensitivity analysis, was adopted at Step 4 in November 2019 and has had effect in the EU since 30 July 2020. On constructing an estimand it puts it this way: “it is important to proceed sequentially from the trial objective and an understanding of the clinical question of interest, and not for the choice of data collection and method of analysis to determine the estimand.” The estimand is defined first, from the clinical question. Only then is an aligned estimator chosen.

Then diagnose support, using the longitudinal checks rather than the point-treatment ones. Estimate the policy contrast last.

Run it the other way round — fit first, then ask what was estimated — and you get the case at the top of this lesson: a clean-looking number that nobody can say the meaning of. In regulated work you also get an analysis whose ordering an adopted guideline explicitly warns against.

No single g-method is better than the others in general, and looking for one is a way of avoiding the real question. What separates them is where each concentrates its modelling risk.

A marginal structural model puts the weight of the argument on the treatment and censoring models. Get those wrong and the pseudo-population is wrong, however tidy the final fit looks. Cole and Hernán's ladder is that risk made visible: six defensible answers from one dataset, separated only by a choice about weights.

G-computation moves the risk onto the outcome and covariate models. It has to simulate the world forward, and it will happily simulate a world that could not exist. 78,746 women in the Nurses' Health Study, followed over 1982–2002, were the first large-scale epidemiologic application of the parametric g-formula, published in the International Journal of Epidemiology in 2009. The observed 20-year risk of coronary heart disease in that cohort was 3.50%. The abstract reports what the simulation gave instead: “Under a joint intervention of no smoking, increased exercise, improved diet, moderate alcohol consumption and reduced body mass index, the estimated risk was 1.89% (95% confidence interval: 1.46-2.41).” Hold the two figures apart. The 3.50% was measured on 78,746 real women. The 1.89% was read off a simulated population, generated by the fitted covariate and outcome models, under a five-part intervention nobody in the cohort was assigned to. Both are numbers. Only one of them is an observation.

G-estimation asks you to get the shape of the blip right as well as the treatment model.

So the ranking is not a property of the methods. It is a property of your system, and of which parts of it you can honestly claim to know.

Take a single dynamic treatment problem — one where the rule responds to the patient's evolving state rather than fixing the treatment in advance. There is a published one to work against. The HIV-CAUSAL Collaboration ran it in Annals of Internal Medicine in 2011, and states its design in one sentence: “Prospective observational data from the HIV-CAUSAL Collaboration and dynamic marginal structural models were used to compare cART initiation strategies for CD4 thresholds between 0.200 and 0.500 × 10(9) cells/L.” That is the shape of the exercise: a rule that fires when a measured state crosses a line, compared against other lines.

Start with the two sample sizes, because they are the exercise in miniature. Of 20,971 therapy-naive HIV-infected people, 8,392 entered the analysis. Everything downstream is a statement about the second number. The distance to the first is what requiring usable histories costs.

Then read the two outcomes against each other. Against the 0.500 threshold, the mortality hazard ratio was 1.01 (95% CI 0.84–1.22) at 0.350 and 1.20 (0.97–1.48) at 0.200. For AIDS-defining illness or death it was 1.38 (1.23–1.56) at 0.350 and 1.90 (1.67–2.15) at 0.200. Same people, same strategies, same weights. On mortality the 0.350 threshold is indistinguishable from 0.500. On the composite outcome it plainly is not. The choice of outcome moved the conclusion further than the choice of method will.

Now implement a second method on that same question. Hold the strategy, the covariate history and the horizon identical, so that the only thing changing is where the modelling sits. Record, for each one, the point at which a model is carrying the answer: the treatment and censoring models for the weighted route, the simulated covariate paths for the g-formula route. Those are the places where the estimate is a claim about the model rather than a reading of the data. Seeing both versions side by side is the fastest way to find them.

The four have been circling each other since the case. They are easy to blur, because they answer the same question and share the same assumptions. What distinguishes them is what each one actually models. Each also has a published analysis behind it you can go and read.

Reach for a marginal structural model when you can credibly estimate how treatment and censoring were determined at each step, and when the quantity you owe someone is a marginal comparison between strategies. Reach for g-computation when the outcome and the evolution of covariates are the parts you can model with a straight face. Consider a structural nested model when the effect is naturally expressed as a blip at each moment, or when the regimes you care about are dynamic.

The HIV-CAUSAL question was in fact answered twice, on one dataset, by two g-methods. That makes it the right place to test what agreement is worth. The same 8,392 individuals went through the parametric g-formula instead of IP weighting, in a 2011 analysis by Young and colleagues. The 5-year mortality risks came out at 2.65% (95% CI 2.15–3.43) for the CD4 500 threshold, 3.06% (2.59–3.67) for 350 and 3.65% (3.01–4.44) for 200. The ordering matches the weighted analysis and the intervals are narrower. They say plainly what bought the narrowing: “However, estimators based on the parametric g-formula are more efficient than IP weighted estimators. This is often at the expense of more parametric assumptions.”

So the tempting move at the end — run two methods and treat their agreement as confirmation — is encouraging, and it is not proof. Those two analyses rest on the same 8,392 histories, the same sequential exchangeability assumption and the same gaps in support. The 12,579 people who did not enter the analysis are missing from both of them equally. What the pair does settle is where each method spends its risk. The weighted route bought wider intervals and asked less of the outcome model. The g-formula route bought narrower ones and asked more. That is a real finding about the two estimators. It is not a second measurement of the world.