Why Changing Standard Care Can Change the Comparison
In a platform trial, an arm may recruit while background therapies, supportive care, or clinical management are changing. A new prophylactic treatment might reduce complications for all patients; a revised supportive-care protocol might change toxicity; or clinicians might adopt a new co-therapy at different rates over time. These changes can alter outcomes even if the study treatment has no effect. If the study arm and its controls experience different care contexts, their outcome contrast may mix the effect of the study treatment with the effect of changing standard care.
The key is to state which effect is wanted. A treatment effect under a specified version of standard care is not automatically the same as the effect of adding the treatment to the mix of care patients receive during an entire platform’s recruitment. The earlier material on time-specific treatment-effect estimands provides the general framing; here the focus is on making background care explicit in the comparison.
The context \(C\) must be defined substantively. It might represent whether a background therapy was available, a protocol-defined care policy, or a documented practice regime. Calendar period can help locate a change, but it is not itself proof that every patient received the same background care. If uptake varies within a period, an era indicator may not capture the relevant exposure.
A target effect can average context-specific effects over a stated distribution \(g(c)\):
This is the average effect for the chosen mix of background-care contexts. Choosing \(g(c)\) is part of defining the estimand: it might represent current practice, the mix in a specified patient population, or equal weight across the contexts of interest. If effects differ by context, there is no single context-free treatment effect without specifying how contexts are combined.
Identification: What Makes a Comparison Credible?
The cleanest evidence comes from randomizing the study treatment and control concurrently within the relevant care context. If assignment is randomized within \(C=c\), the assigned groups are comparable in expectation with respect to their potential outcomes in that context. The within-context contrast can then identify \(\tau(c)\), subject to consistency, appropriate outcome ascertainment, and the trial’s other design assumptions.
When controls from different periods are combined, identification requires more. In an observational comparison, conditional on measured covariates \(X\) and care context \(C\), treatment assignment must be exchangeable with the potential outcomes being compared. There must also be positivity: within each context and covariate pattern given weight in the target, patients must have a nonzero chance of receiving each comparison treatment. Adjustment cannot recover a treatment effect in a context where one arm was never observed.
Care variables also require careful timing. A background-care policy already in force at randomization, or a common co-intervention assigned independently of study-arm assignment, may be used to define strata or adjustment variables. But a therapy delivered after randomization that can be changed by the study treatment may be a mediator. Adjusting for it can remove part of the treatment effect or introduce bias. The relevant question is not merely whether a variable is called “standard care,” but when it occurs and whether assignment to the study arm can affect it.
A Decomposition of the Crude Contrast
The following identity shows why different care mixes can distort an unadjusted contrast. Let \(p_a(c)=P(C=c\mid A=a)\) be the distribution of care context among patients assigned to arm \(a\), and let \(\mu_a(c)\) denote the context-specific outcome risk. The observed arm-specific risks, if the context-specific risks are identified, are averages over each arm’s own context distribution. Subtracting those averages gives:
To verify the identity, expand the right-hand side. The terms \(-\sum_c p_1(c)\mu_0(c)\) and \(+\sum_c p_1(c)\mu_0(c)\) cancel, leaving \(\sum_c p_1(c)\mu_1(c)-\sum_c p_0(c)\mu_0(c)\). The first component is a treatment contrast averaged over the treated arm’s care mix. The second is a care-composition component: it is nonzero when the arms have different context distributions and control outcome risks vary across contexts.
This is an algebraic decomposition, not a guarantee of causal identification. For the first component to represent causal effects, the context-specific risks must be identified under suitable assignment assumptions. If an arm has no observations in a context, the missing context-specific comparison cannot be supplied by the identity.
Worked Example: How Different Care Mixes Distort a Risk Difference
Suppose a hypothetical platform comparison has two recorded care contexts: an earlier context and a later one after a beneficial background therapy became common. The treatment group has 50 earlier-context patients with 10 events and 150 later-context patients with 18 events. The control group has 150 earlier-context patients with 45 events and 50 later-context patients with 7 events. Assume, for this illustration, that the within-context comparisons are otherwise valid.
The crude treatment risk is \(28/200=0.140\), and the crude control risk is \(52/200=0.260\). The crude risk difference is:
The context-specific risks are \(10/50=0.200\) versus \(45/150=0.300\) in the earlier context, giving a risk difference of \(-0.100\), and \(18/150=0.120\) versus \(7/50=0.140\) later, giving \(-0.020\). Standardizing both arms to an equal mix of the two contexts gives:
Thus, the crude difference is a 12.0 percentage-point lower event risk, while the equal-mix standardized difference is 6.0 percentage points lower. The crude contrast gives the two arms different weights on care contexts, so it does not answer the equal-mix question. This calculation does not establish that the standardized result is causal by itself: that interpretation still relies on valid within-context comparisons and adequate overlap.
Use a Defined Target Mix and Check Overlap
Stratification and standardization make the target comparison explicit. Estimate the treatment and control risks within each care context, then average each arm’s risks over the same target weights \(g(c)\). Subtract those standardized risks to obtain the target risk difference. Using the same weights is essential: otherwise, the arm contrast still combines treatment effects with differences in context composition.
Worked Example: Standardizing to Current Practice
In a separate hypothetical comparison, the earlier-care context has 100 patients per arm: 15 treatment-arm events and 25 control-arm events. The current-care context has 200 patients per arm: 24 treatment-arm events and 28 control-arm events. Suppose the target population is defined to be 25% earlier care and 75% current care.
The context-specific risks are \(0.15\) and \(0.25\) under treatment and control in earlier care, and \(24/200=0.12\) and \(28/200=0.14\) in current care. The standardized risks are:
For this target mix, the estimated event risk is 4.00 percentage points lower under treatment than control. This is an average over the specified 25%/75% care mix, not an estimate that applies automatically to every care context. The context-specific differences are \(-0.100\) and \(-0.020\), so the effect is more favorable in the earlier-care context in these data.
A model can also include care context and a treatment-by-context interaction. For a binary outcome, a risk-difference model might be written:
With \(C=0\) as the reference context, \(\beta_A\) is the model-based treatment risk difference in that context, and \(\beta_{AC}\) is the difference between the treatment risk differences for \(C=1\) and \(C=0\). This linear probability model is convenient for illustrating risk differences, but its predicted risks can fall outside the interval from zero to one. A model with another link function has a different coefficient interpretation; for example, logistic-regression coefficients are on the log-odds scale and should not be read as risk differences. In either case, report contrasts standardized to the target population when that is the estimand, rather than relying only on a treatment coefficient.
When the Arm and the Care Change Do Not Overlap
Worked Example: A Historical Control Is Not a Current-Care Control
Suppose, hypothetically, 30 of 100 patients in an earlier control cohort experience an event under the old background-care policy. A new treatment arm recruits after a beneficial standard-care change; 18 of 100 patients in that arm experience an event. The crude comparison is \(0.18-0.30=-0.12\), or a 12-percentage-point lower event risk in the new arm.
Now suppose 20 of 100 concurrent control patients receiving current standard care experience the event. The concurrent risk difference is \(0.18-0.20=-0.02\), or a 2-percentage-point lower risk in the treatment arm. The historical control risk is 10 percentage points higher than the concurrent control risk (\(0.30-0.20=0.10\)), consistent with the possibility that background care, or other changes over time, improved control outcomes. The data do not justify attributing the full 12-point historical contrast to the study treatment.
The concurrent comparison is the more direct estimate of adding the study treatment under current care, provided assignment was randomized and other trial conditions are met. The historical comparison cannot isolate treatment from the care change merely by labeling the groups as “control” and “treatment.” If no patients receiving the study treatment were observed under old care, or no controls under current care, the treatment effect in the absent combinations is not identified from these data without additional assumptions.
Diagnostics, Alternatives, and Limitations
Before estimating an adjusted or standardized contrast, document what changed and when. Review protocol and practice changes, the availability and uptake of background therapies, and whether uptake differed between arms or sites. Plot or tabulate outcomes and care-context frequencies by arm and recruitment period. The aim is not to replace the treatment comparison with a trend analysis; it is to discover whether the compared patients faced materially different care and whether there is enough data to compare arms within the relevant contexts.
Define the therapy or practice change, its timing, and whether the variable describes policy, availability, or patient-level receipt.
Choose whether the target is an effect under a particular care context or an average over a stated target distribution.
Check that both comparison arms occur in contexts being targeted, and determine whether care variables precede randomization or may be affected by treatment.
Use concurrent randomized contrasts when available; otherwise, use justified adjustment or standardization and state the assumptions and unsupported contexts.
The main alternatives answer different questions. A concurrent randomized comparison estimates an effect in its enrolled care context without needing to borrow controls from earlier periods. Regression adjustment can account for measured context and covariates, but depends on adequate model specification and overlap. Stratified analysis avoids assuming a single common treatment effect across contexts, while standardization combines those effects for a chosen target mix. Difference-in-differences addresses a different design question about changes over time and requires its own assumptions; it does not automatically correct unequal uptake of a specific background therapy or identify treatment-by-care interaction.
Several warning signs call for restraint: one arm is absent from a care context; estimates change sharply across plausible context definitions; uptake is poorly recorded; or adjustment makes large extrapolations into sparse combinations. Also check whether the apparent care variable is post-randomization and treatment-affected. In these cases, adjusted estimates may look precise while relying on weak or inappropriate assumptions. Sensitivity analyses can show how conclusions depend on unmeasured differences, but cannot create empirical overlap where none exists.
The practical conclusion is not that every change in standard care invalidates a platform comparison. Rather, the treatment effect must be attached to a care context or target distribution, and the data must support the comparison being claimed. When treatment effects vary with background care, a single pooled estimate can conceal clinically important differences; when care distributions differ, it can also reflect composition rather than treatment alone.
Check Your Understanding
Answer each question using the definitions and calculations above. Brief solutions follow.
- Why might a crude treatment-control risk difference be misleading when the arms have different distributions of background-care contexts?
- In a target population that is 60% context 0 and 40% context 1, the treatment risk differences are \(-0.05\) and \(0.02\). What is the standardized risk difference?
- What does it mean for a study arm and care context to lack overlap, and why can regression adjustment not solve that problem without assumptions?
- Why might adjusting for a post-randomization background therapy be inappropriate?
Solutions. 1. The arms average context-specific risks using different weights, so the crude contrast can include a care-composition component as well as treatment effects. 2. \(0.60(-0.05)+0.40(0.02)=-0.030+0.008=-0.022\): a 2.2-percentage-point lower risk on average for the stated target mix. 3. At least one arm has no observations in a context being targeted; the missing contrast is not informed by data, so a model must extrapolate. 4. If assignment can affect receipt of that therapy, it may be a mediator; conditioning on it can remove part of the treatment effect or create bias.