In clinical epidemiology, we sometimes need to estimate the effect of an exposure of interest E (eg, an antihypertensive treatment) on change from baseline of a time-dependent quantitative outcome (eg, blood pressure at time t, denoted as
). The exposure E is observed at the beginning t1 of the study (although it may have occurred before the beginning of the study), and a change score is defined as the difference ΔBP in blood pressure between the beginning t1 and the end t2 of the study:
Two methods of estimating the effect of E on change from baseline have been regularly discussed: computing a linear regression of ΔBP adjusted for baseline value BP(t1) (sometimes called analysis of covariance, when the exposure of interest is categorical) or unadjusted for baseline value (sometimes called “simple analysis of change score”).1 For the individual person i (i = 1, …, I), the linear regression of ΔBP on E adjusted for BP(t1) is as follows:
It is known that the regression coefficient τE can also be estimated using a linear regression of BP(t2) on E adjusted for BP(t1):2
The linear regression of ΔBP on E unadjusted for BP(t1) is as follows:
The causal effect of E on ΔBP is estimated by the regression coefficients
according to the model chosen. In some situations, the models can lead to very different results. This paradox was pointed out by Lord3 in the case of a nonrandomized study exploring the effect of sex on weight change.
In the literature, the choice between a model adjusted or unadjusted for the baseline value of the outcome is usually based on considerations about the design of the study and the regression-to-the-mean phenomena. Regarding study design, Van Breukelen showed that, compared with linear regressions of ΔBP unadjusted for BP(t1), adjusting for BP(t1) provides more power in randomized studies but may be more biased in nonrandomized studies.4 Senn also showed the value of adjusting for baseline outcome level to obtain unbiased estimates of the exposure in randomized studies as well as in “cutoff designs” (studies in which subjects are allocated to one of the exposure groups according to their baseline value). In addition, he stated that in observational studies where baseline values are different between exposure groups, both adjusted and unadjusted models for BP(t1) would probably give biased results.1
This regression-to-the-mean phenomenon results from intraindividual variability and measurement error on the baseline outcome value (a short illustration is given in the eAppendix; http://links.lww.com/EDE/A839).5,6 Based on directed acyclic graphs (DAGs) and in the case of a nonrandomized study, Glymour et al7 showed that adjusting for baseline outcome level could lead to a biased estimate when the outcome is measured with error, whereas models unadjusted for baseline level could give unbiased results. Van Breukelen4 indicated that in the case of “cutoff design” studies, regression-to-the-mean results in a spurious association between the exposure and change from baseline, which is correctly controlled by adjusting for baseline value, but is ignored with unadjusted linear regressions. On the contrary, in nonrandomized studies with baseline values that differ between preexisting exposure groups, there are some situations in which not adjusting for baseline value rather than adjusting gives unbiased estimates. Generally, any spurious association between E and change ΔBP (ie, not resulting from a direct or indirect effect of E) needs to be controlled.
It is interesting to point out that all these recommendations depend on the causal relation between the exposure E and the baseline level of the outcome BP(t1).
Beyond adjusting for the baseline value of the outcome, it is worth considering the role of other relevant factors in the analysis. For example, Glymour et al7 mentioned factors occurring before the beginning of the study which can influence the outcome BP(t1) at time t1 as well as change of the outcome during the study. They showed how this “horse-racing effect” (using Peto’s expression)8 can bias the estimation of the effect of E on change when computing a linear regression adjusted for baseline level. Clarke9 explicated a typical example in which age at the beginning of the study could be a causal factor for both the baseline value of the outcome and change from baseline. Under certain functional hypotheses, he suggested inclusion of E × age(t1) interaction terms in models of change from baseline when estimating the causal effect of E on change.
All these elements are related to the underlying causal structure, which can be described explicitly by DAGs. Applying DAGs more systematically in studies of change from baseline could be useful in guiding the statistical analyses.
Our aim was to guide the choice of a statistical model (linear regression, adjusted or unadjusted for baseline outcome level) to estimate the causal effect of an exposure on change in outcome, using DAGs to represent a wide range of situations characterized by various study designs, regression-to-the-mean phenomena, and other relevant variables, such as pre-existing common factors (such as age) or additional confounders. We used graphical rules (like the d-separation rule) to interpret DAGs. These rules enable the analyst to identify potential biases when computing a model adjusted or unadjusted for the baseline blood pressure level. In general, estimating causal effects from variables measured with error can result in measurement bias. However, under additional structural and functional assumptions (no measurement error on the exposure E, outcomes following an approximately Gaussian distribution with a sufficiently large sample size and assuming a classic error measurement scheme as described below), path analysis principles can be applied in complement to DAG rules to show how the causal effect of interest between the exposure E and the latent change from baseline ΔBP could be estimated unbiasedly from the observed change from baseline ΔBP* despite error on BP measurement.
Along with the graphical interpretation, we simulated data sets compatible with the causal structure of the DAGs and estimated the effect of the exposure on change applying both types of linear regression. Generation of the simulated data sets is described in the eAppendix; http://links.lww.com/EDE/A839, detailing the links between DAGs and algebra, and the links between models of change from baseline (ΔBP) and models of an outcome at a given time (BP(t)).
For simplicity, we will deal with a binary exposure (E = 1 for exposure vs. E = 0 for nonexposure). We focused on the situation of a complete and equal follow-up for every participant; in the case of variable follow-up, one would have to discuss additional hypotheses about independence of the length of follow-up with other variables in the system.
This article is organized according to the causal relation between the exposure E and the baseline level of the outcome BP(t1). The next section focuses on randomized studies. Next, we describe the case of nonrandomized studies with confounding factors influencing the exposure E,
and ΔBP. Following that, we describe the case of nonrandomized studies in which the observed baseline value of blood pressure influences the exposure E (“cutoff designs”). Then, we describe nonrandomized studies where the exposure starts before the beginning of the study. Finally, discussion and concluding remarks are given.
We will use the following notations for two variables X and Y:
is the path coefficient of X→Y,
is the variance of X, and
is the covariance between X and Y.
Figure 1A and B represents two causal structures corresponding to randomized trials. The exposure E is independent of the baseline blood pressure BP(t1) because of randomization. The outcome ΔBP is defined by the function
. The manner in which the three variables BP(t1), BP(t2), and ΔBP could be represented in a DAG has been subject to debate.10 Because of the deterministic nature of the relation among ΔBP, BP(t1), and BP(t2) whatever the level of the exposure E:
- BP(t2) and E are always conditionally independent given BP(t1) and ΔBP, and
- ΔBP and E are always conditionally independent given BP(t1) and BP(t2).
The “inductive causation algorithm” described by Pearl11(ch. 2) can be used as a tool to recover DAG structures from conditional independence relation. Pearl states that a pair of variables A and B cannot be connected by an edge if a set of variable SAB can be found such that A and B are conditionally independent given SAB. Consequently, we can neither draw any direct effect from E to BP(t2) nor from E to ΔBP in a DAG including all four variables: BP(t2) has to be deleted from a DAG showing E, BP(t1), and ΔBP to represent the causal effect of E on change ΔBP. It is possible to depict a causal structure showing E, BP(t1), and BP(t2) (without ΔBP), but such a DAG is not much help in encoding the relation between E and ΔBP. Examples of algebraic relation between the effect of E on ΔBP and the effect of E on BP(t2) are detailed in the eAppendix; http://links.lww.com/EDE/A839.
From the DAG of Figure 1A, one can discuss the possibility that BP(t1) influences ΔBP (such as through an intermediate and unmeasured mechanism represented by the variable M in Figure 1B).
In the DAGs in Figure 1, we added a set of pre-existing variables P with a causal influence on both BP(t1) and ΔBP. For example, the set P can include age at the beginning of the study (
) which can be used to model the natural evolution of blood pressure with aging, as in the simulated examples (in this approach, we assume no cohort effects to simplify the model).
We used the notation
and ΔBP* for the observed blood pressure and change values, respectively.12 The observed blood pressure is influenced by the unmeasured (latent) blood pressure BP(t1) and BP(t2) and intraindividual terms denoted UBP1 and UBP2 (which can include intraindividual variability and measurement error). We assume that
are defined according to a classic measurement error scheme in which
- UBP1 and UBP2 are independent exogenous variables from a Gaussian distribution of mean 0 and variance
The observed change score is denoted ΔBP* and is defined by
. From the assumptions regarding functional relation among BP(t1),
, ΔBP, and ΔBP*, we have the following path coefficients values:
. Because we estimate the causal effect of the exposure on ΔBP from the observed variable ΔBP*, the regression models become:
- adjusted for baseline level:
- unadjusted for baseline level:
where the effect of the exposure on the observed change score is estimated by coefficients
and where the functions ϕ and ϕ' can include interaction terms between E and age(t1) as in the simulated examples.
Graphical rules and conditions for interpreting DAGs and identifying causal effects are described elsewhere.11,13 To facilitate the interpretation of the DAGs, readers can delete the arrow E→ΔBP (showing the null hypothesis). Applying these graphical rules in causal structures of Figure 1, we can see that the causal effect of the exposure E on change ΔBP corresponds to the direct path E→ΔBP. As there is no unblocked back-door path between E and ΔBP, the potential expectation of ΔBP that would be observed if E was fixed to E = e,
(using Pearl’s notation) is identifiable; it can be estimated by
, indicating that the causal effect of E on ΔBP can be estimated by the coefficient
of the linear regression unadjusted for BP(t1) (model 2).11 The coefficient
cannot be estimated directly using model 2 because ΔBP is unobserved; however, by applying a path analysis we can easily show that
is estimated using model 4 with the observed change score ΔBP*.14 In addition, adjusting for
does not activate any back-door path between E and ΔBP*, and thus
and the causal effect of E on ΔBP could be estimated without bias by adjusting for BP*(t1) in linear regressions (model 3) as well as without adjusting for BP*(t1) (model 4).
The mean bias and standard error of the effect of E on ΔBP estimated from model 3 and model 4 applied on the simulated data are described in the Table. Both models gave unbiased estimations of the effect of E on ΔBP in causal structures of Figure 1, with smaller standard error using the linear regression adjusted for BP*(t1). The greater power of this model was an expected result in randomized trials.4 Vickers15 showed that:
- power increases on an absolute scale for both models when the correlation between baseline and follow-up values is higher;
- with smaller correlations between baseline and follow-up values, baseline-adjusted models are comparably more efficient than the unadjusted models.
Nonrandomized Studies with Confounding Factors Between the Exposure and the Outcome
In Figure 2A and B, the two initial causal structures have an additional baseline confounder (or a set of confounders) C that influences the exposure E as well as BP(t1) and ΔBP. As in the previous section, pre-existing variables P (such as age at the beginning of the study) can influence BP(t1) and ΔBP. Interestingly, when confounders C have the same effect on BP(t1) as on BP(t2), they do not affect change over time in blood pressure so that Figure 2A and B can be simplified into the structures of Figure 2C and D. One could consider these causal structures under some additional functional assumptions such as no modification of the effect of C on BP(t) over time. Because the situation of common causes of E and BP(t) does not equate to common causes of E and ΔBP, simplifying the causal structure might not appear straightforward.
When All Baseline Confounders C Are Measured
In such a situation, we can block all back-door paths between E and ΔBP*. The causal effect of E on ΔBP* is thus identifiable and we can estimate without bias the effect of E on ΔBP using linear regression analyses adjusted for the confounders C, whether or not BP*(t1) is adjusted for. Assuming no effect modification by C, we would use the following models:
- – adjusted for baseline level:
- – unadjusted for baseline level:
When Some Baseline Confounders C are Unmeasured
In this case, the estimation of the causal effect of the exposure E on ΔBP is expected to be biased, with the notable exception of applying a regression unadjusted for BP*(t1) in Figure 2C:
- (i) Applying a linear regression adjusted for BP*(t1) but unadjusted for some unmeasured confounders C (model 3), the estimation of the effect of E on ΔBP by
- is expected to be biased due to the following back-door paths in all structures of Figure 2:
- • the back-door path resulting from adjusting for the collider
- , which creates a spurious correlation between BP(t1) and UPA1: E←C→BP(t1) - - - UPA1→ΔBP*;
- • two potential back-door paths that cannot be blocked if C and M are unmeasured: E←C→ΔBP→ΔBP* in Figure 2A and B, and E←C→BP(t1)→M→ΔBP→ΔBP* in Figure 2B and D.
- (ii) Applying a linear regression model unadjusted for BP*(t1) (model 4), the estimation of the effect of E on ΔBP by
- is expected to be biased because of the following back-door paths in Figure 2A, B, and D where C and M are unmeasured:
- • the unblocked back-door path E←C→ΔBP→ΔBP* (Figure 2A and B);
- • the unblocked back-door path E←C→BP(t1)→M→ΔBP→ΔBP*(Figure 2B and D).
- (iii) However, in the causal structure depicted in Figure 2C, there are only two back-door paths between E and ΔBP*: E←C→BP(t1)→BP*(t1)←UBP1→ΔBP* and E←C→BP(t1)←P→ΔBP→ΔBP*. These back-door paths are blocked when one does not condition on BP*(t1) so that the causal effect of E on ΔBP could be estimated unbiasedly by the coefficient
- applying an unadjusted regression for the baseline value of the outcome (model 4), despite the unmeasured set of variables C.
In the Table, we show illustrative results from simulated data sets compatible with the causal assumptions in Figure 2, where C is a binary unmeasured confounder with no modification of the effect of E by C, and where the direct effect of C→BP(t) is either modified by age(t1) (Figure 2A) or unmodified by age(t1) (Figure 2C and D). These results are consistent with the above graphical interpretation completed by path analysis. We did not simulate data from Figure 2B as they would not provide additional information to the simulations from Figure 2A and D.
Nonrandomized Studies in Which the Observed Baseline Outcome Influences the Exposure
In Figure 3A and B, we add a causal influence from the observed blood pressure
to the exposure E in the causal structures of Figure 1. For example, an antihypertensive treatment may be more frequently given to patients with higher observed blood pressure at the beginning of the study. Such a causal structure also corresponds to the cutoff design mentioned by Senn.1
The estimate of the causal effect of E on ΔBP is expected to be biased using a linear regression unadjusted for BP*(t1) (model 4), because the association between E and ΔBP* estimated by the coefficient
corresponds to the indirect path of interest E→ΔBP→ΔBP* and one or two unblocked back-door paths:
- – E←
- ←UBP1→ΔBP* in Figure 3A and B;
- – E←
- ←BP(t1)→M→ΔBP→ΔBP* in Figure 3B.
Another back-door path is present in Figure 3A and B, E←
←BP(t1)←P→ΔBP→ΔBP*, but it can be blocked by adjusting for P.
In using the linear regression analysis adjusted for baseline level (model 3), the adjustment for
blocks all these back-door paths and the estimated coefficient
is only explained by the indirect path E→ΔBP→ΔBP*. The causal effect of E on ΔBP could be estimated without bias by the coefficient
, as we can see by applying the following path analysis:
Consistent results from simulated data sets compatible with the causal assumptions in Figure 3A and B are presented in the Table.
This situation could be extended to a causal structure in which pre-existing measured values of the “outcome” variable confounds the relation between E and change from baseline. A simple example is given in Figure 3C, where BP(t0) is a pre-existing value of blood pressure, BP*(t0) rather than BP*(t1) influences E, and the set of pre-existing variables P could include an age variable age(t0). These variables BP*(t0) and P are not usually collected and are therefore unavailable for analysis. In this DAG, the back-door path E←BP*(t0)←BP(t0)←P→ΔBP→ΔBP* connects E to ΔBP*. If BP*(t0) and P are unmeasured, it cannot be blocked by adjusting for BP*(t1), resulting in a bias when estimating the causal effect of E on ΔBP* using model 3. In the simulated data set derived from Figure 3C, we can see that computing models 3 or 4 gave biased estimations of the causal effect of E on ΔBP (Table). In the example of Figure 3C, one could adjust for BP*(t0) to get an unbiased estimation of the causal effect of E on ΔBP. In a more general way, it can be useful to characterize the pre-existing evolution of the “outcome” variable.16
A final point on cutoff designs is that the positivity assumption should be examined carefully. This assumption is needed to identify causal effects; it holds when the probability of being exposed to every level of exposure is greater than zero for every combination of the values of the confounders in the population.17 For example, there is a clear positivity violation in a cutoff design where all subjects with BP*(t1) < 150 mmHg are unexposed to E and all subjects with BP*(t1) ≥ 150 mmHg are exposed to E. The positivity violation can be examined using propensity scores or by a descriptive tabular analysis of the exposure according to combinations of confounder values.17
Nonrandomized Studies in Which the Exposure Starts Before the Beginning of the Study
In Figure 4, the causal structures differ from the previous ones by an exposure that starts before the beginning of the study and influences both BP(t1) and ΔBP, as in the examples given by Lord and Glymour et al.3,7
In the causal structures of Figure 4, there is no unblocked back-door path between the exposure E and the observed change score ΔBP*. The effect of E on ΔBP is explained by one or two paths, resulting in a causal effect equal to
- – E→ΔBP in Figure 4A and B;
- – and E→BP(t1)→M→ΔBP in Figure 4B.
This effect could be estimated without bias by the coefficient
using a linear regression unadjusted for BP*(t1) (model 4):
Using the linear regression analysis adjusted for BP*(t1) (model 3), a spurious correlation between BP(t1) and UBP1 is created and adds a back-door path between E and ΔBP*: E→BP(t1) - - - UBP1→ΔBP*. This back-door path biases the estimation of the causal effect of E on ΔBP, as it is included in the association estimated by the coefficient
of model 3.
Results from the simulated data sets were consistent with the graphical interpretation (Table).
The approach, based on DAGs with some functional hypotheses to carry out path analyses, confirms the lack of bias in randomized studies, whatever the chosen model. It clarifies why adjusting for the observed baseline outcome value can be recommended in many studies in which the baseline outcome influences the exposure (Figure 3). The particularities of the causal structures in Figure 3 (including cutoff designs) may not have been widely highlighted in the epidemiologic literature. They are contrasted with structures of Figure 4 (where the exposure starts before the beginning of the study), in which using linear regression unadjusted for the baseline value appears to be the best choice. Finally, the approach points out critical assumptions to be discussed when some variables confound the exposure–outcome relation (Figure 2).
In our view, randomization, confounding through a third variable (C) or the observed outcome
at the beginning of the study, start of the exposure, natural evolution of the outcome in time, and intraindividual variability are the main points to discuss. Of course, all of the possible causal structures cannot be reduced to the few situations described above. In particular, more complex combinations implying confounders between the exposure and the outcome (as in Figure 2) were not described above:
- (i) Confounding between the exposure E and change ΔBP through confounders C and through the observed
- (combining Figures 2 and 3). In such a case, one has to adjust for the baseline outcome level, as well as for the set of confounders C. Bias is most likely inevitable if C contains unmeasured variables that cannot be adjusted for.
- (ii) An early exposure E before the beginning of the study, and confounding between E and change ΔBP through variables C (combining Figures 2 and 4). In such a case, one has to apply a linear regression model unadjusted for the baseline outcome level, but adjusted for variables C. Combining Figures 2C and 4A, under the assumption of no effect modification of C on blood pressure over time, a linear regression analysis unadjusted for BP*(t1) could still give an unbiased estimation even if some variables in C are unmeasured.
Many of the causal assumptions represented in Figures 1–4 rely on the analyst’s judgment rather than on observed data.
- The assumption that there are no unmeasured confounders C in Figure 2 is typically untestable.
- More complex measurement errors can be represented in DAGs and should be discussed. For example, one might draw a direct causal influence from BP(t1) to UBP1 to take into account ceiling or floor effects.7 One could consider some dependent (with a common parent of UBP1 and UBP2) or differential measurement error (with a causal effect of E on UBP1 or UBP2).12 These measurement errors could add some bias according to the underlying causal structure and the applied estimation method.
- A challenging assumption concerns the potential influence of BP(t1)→ΔBP. Such an assumption will usually be drawn from pathophysiologic knowledge. Furthermore, one could consider that a nonlinear functional model would be more appropriate to model BP change in that case.
Another recurrent question relates to the effect modification of E on change ΔBP by the baseline outcome BP(t1) (or, more pragmatically, by the observed value
). Following the classification provided by VanderWeele et al,18
could be an effect modifier by proxy or by common cause in Figures 1–3 on ΔBP. In these situations, effect modification by
can be estimated by applying a linear regression adjusted for
and appropriately adjusted for the confounders C and pre-existing variables P. BP(t1) or
cannot be an effect modifier in the causal structures of Figure 4 because they are descendants of the exposure E (Theorem 1 in VanderWeele et al18).
Although our paper has focused on linear regressions, the causal structures depicted in Figures 1–4 could also be used to consider adjusting for BP*(t1) in a logistic regression or a time-to-event model when the outcome is defined from ΔBP (eg, Y = 1 if ΔBP <−5 mmHg, Y = 0 otherwise). However, because these are nonlinear models, path analysis principles should not be applied, and the estimated causal effect could still be distorted due to measurement error. Analyses of change from baseline are complex, and using DAGs turns out to be a very useful approach to choosing the most appropriate linear model. As these tools rely on partly untestable assumptions (such as unmeasured confounding), the analyst should attempt to gather meaningful arguments to discuss them. Among other approaches, one can test some independence or conditional independence relation to check whether the observed data are compatible with the assumptions depicted in the DAG. Intra-individual variability and measurement error could be explored through reviews of the literature or repeated measures of the outcome at a given time in a subsample of the study population. In some cases, corrective methods can be implemented.7 Plots of the outcome against age can give indications of the general shape of the outcome evolution and guide the choice of a functional relation between the exposure and the change score. Several alternative causal structures can be examined to look for potential biases and carry out sensitivity analyses.
We thank Nina Crowte, Mary Iagnemma, and Michelle Kelly-Irving for correcting English grammar and spelling.