DAGs and Target Trial Emulation for Oncology Management Research: Eight Causal Chains

Almost a third of the oncology management literature (27% of an 856-article corpus) reports “adjusted” analyses, yet the reasons for choosing the adjustment set are rarely given. Which variables should enter the model, which must stay out, and which unmeasured factors quietly undermine the conclusion? This chapter answers those questions for the eight candidate causal chains identified in the companion causal chain analysis. For each chain it draws an explicit directed acyclic graph (DAG), derives minimal sufficient adjustment sets algorithmically with Pearl’s back-door criterion, identifies mediators and colliders that must not be adjusted for, shows where unmeasured confounding breaks identification, writes a target trial emulation protocol, and demonstrates the consequences with simulations.

Method in brief

Each DAG was built from the earlier inventory of 69 variables, with 10 to 17 nodes per chain. Every graph includes measured confounders, mediators, collider or selection nodes, and at least one unmeasured node (U) representing the most plausible threat in that setting: confounding by indication, the healthy-user effect, patient preference or safety culture. Minimal adjustment sets were found by testing d-separation across all subsets of measured non-descendants of the exposure. Target trial protocols specify eligibility, strategies, assignment, time zero, follow-up, outcome and contrast, following the Hernán and Robins framework. Three simulations use synthetic data only; their purpose is to make the consequences of DAG-based decisions concrete, not to analyse the corpus.

Identifiability: the main finding

Only in two chains (Z1 and Z3) are the measured variables sufficient to identify the total effect. In the remaining six, an unmeasured node leaves a back door open. This is not a failure of the analysis but its central contribution: it is now visible which chain rests on the assumption of “no unmeasured confounding”, and those chains can be directed toward sensitivity analysis (E-values, quantitative bias analysis, negative controls) or toward design solutions (randomised trials, interrupted time series or difference-in-differences, active comparators, instrumental variables).

Chain by chain

• Z1. IMRT/VMAT to toxicity to quality of life. Adjust for age, stage, performance status, histology, facility type, calendar year and baseline quality of life. Do not adjust for toxicity (a mediator) when estimating the total effect, nor for plan quality. Loss to follow-up is a selection node: complete-case analyses open collider bias.
• Z2. Hypofractionation to capacity and resource use to cost. The adjustment set (age, stage, histology, comorbidity, facility type, distance, insurance, year) is sufficient only if patient preference is not an unmeasured confounder, so estimates need an E-value or negative control. Patient satisfaction is a common effect of the exposure and patient preference: conditioning on it, for example by analysing only satisfied patients, creates a spurious path.
• Z3. First-line immune checkpoint inhibitors to response and PFS to overall survival. Adjust for PD-L1, age, performance status, metastatic burden, autoimmune comorbidity, line of therapy, year, facility and insurance. Immune-related adverse events are both a mediator and a collider (linked to an unmeasured immune phenotype), so “survival among patients who developed irAEs” analyses are biased. Defining time zero at the first dose prevents immortal time bias.
• Z4. Self-management education to self-efficacy to adherence to quality of life. Identification depends on unmeasured motivation. Programme completion is a collider: per-protocol analyses of completers open the motivation path, so intention-to-treat or inverse-probability-of-censoring-weighted per-protocol analyses are required.
• Z5. Treatment delay over 30 days to stage progression and completion to survival. Delay is a time-varying exposure, and patients must survive long enough to receive delayed treatment, creating immortal time. A clone-censor-weight design is mandatory. Frailty is the unmeasured threat, partly closed through performance status; treatment intensity is a collider.
• Z6. MDT discussion to guideline adherence and timeliness to survival. Confounding by indication (complex cases go to the board) may remain unmeasured; stage and performance status close it partially. Sensitivity analysis with negative control outcomes and E-values, and cluster-robust standard errors for centre effects, are needed.
• Z7. AI auto-segmentation to plan quality and workload to safety events. If the outcome is measured only through reported incidents, a measurement collider appears: AI novelty raises reporting while safety culture affects both reporting and real events. An interrupted time series is recommended to handle secular trends.
• Z8. Exercise programme to symptom burden to unplanned admission. The healthy-user effect is the main threat in observational exercise studies; programme completion is again a collider, so per-protocol analysis is biased.

Target trial emulation principles

Every protocol follows the same rules: time zero, eligibility and strategy assignment coincide (preventing immortal time bias); strategies are predefined and feasible; mediators and colliders are never conditioned on; per-protocol analyses use artificial censoring with inverse probability of censoring weights; and each protocol carries a sensitivity component for unmeasured confounding.

What the simulations show

S1, adjustment choices (n = 20,000). The true total effect of IMRT on 12-month quality of life was set at 4.17 points (3.0 direct plus about 1.2 through reduced toxicity). The naive difference was 6.26, inflated by confounding. The DAG-based back-door set gave 3.86. Adding toxicity, a mediator, gave 2.82, close to the controlled direct effect, showing why “toxicity-adjusted” quality-of-life analyses common in the literature measure the direct, not the total, effect. Analysing only patients who completed follow-up gave 3.74, a selection-collider bias.

S2, cost effect with IPTW and g-formula (n = 15,000). The true average effect of hypofractionation on cost was set at -2,500 currency units. Because early-stage patients are both more likely to receive hypofractionation and cheaper to treat, the naive difference (-4,010) overstated savings by 60%. Propensity-weighted (IPTW) and parametric g-formula estimates (-2,487 and -2,471) converged on the truth, with positivity satisfied.

S3, delay strategies with clone-censor-weight (n = 30,000). True three-year survival was 0.538 for “start within 4 weeks” and 0.505 for “start in 5 to 12 weeks”, a difference of +0.033 favouring early start. The typical literature design, comparing treated patients by their actual delay group, gave 0.511 versus 0.563: the sign reversed and delay looked protective, because patients treated late had by definition survived the first weeks. Cloning each patient into both strategies, censoring at deviation and weighting recovered the true direction and size (0.541 versus 0.496).

Three common errors made visible

• Reporting a “total effect” while conditioning on mediators such as toxicity or response.
• Conditioning on colliders such as immune-related adverse events, treatment completion or clinical trial participation.
• Taking the treatment date as time zero in delay studies, thereby manufacturing immortal time.

Recommendations and limitations

Adjustment sets can now be justified and copied directly into methods sections. In the six chains relying on an unmeasured confounder, point estimates should never be reported alone; E-values, negative control outcomes or active-comparator designs should be standard, and where implementation is staggered (Z6, Z7), interrupted time series or stepped-wedge designs identify effects independently of U. Next steps include piloting a clone-censor-weight design for Z5 with Turkish cancer registry and reimbursement data, an IPTW plus g-formula analysis of Z2 with TDABC-based cost data, and re-analysing Z4 structural equation studies with counterfactual mediation definitions. DAGs rest on domain knowledge and cannot be verified from data: a different edge set yields different adjustment sets, which is why DAGitty code is supplied for debate. Simulations illustrate mechanisms, not real effect sizes.

Source chapter: Kurutkan, M. N. (2026). DAG-based causal identification and target trial emulation for eight causal chains in the oncology management literature. Oncology Hospital Management Training Series, supplementary chapter (original in Turkish). Accompanied by adjustment-set and protocol workbook and simulation code.

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