Yasutaka Chiba

*Division of Biostatistics, Clinical Research Center, Kinki University School of Medicine, Japan* 

#### **1. Introduction**

In human clinical trials, ethical considerations for study subjects override the scientific requirements of trial design. Noncompliance with an intervention or study procedure for ethical reasons is thus inevitable in practice (Piantadosi, 1997).

The Coronary Drug Project (CDP) trial (CDP Research Group, 1980) was a typical example of trials with noncompliance. The CDP trial was a large, double-blinded, randomized trial testing the effect of the cholesterol-lowering drug, clofibrate, on mortality. Patients were randomly assigned to the clofibrate or placebo groups and were followed for at least 5 years, documenting clinic visits and examinations. During each 4-month follow-up visit, the physician assessed compliance by counting or estimating the number of capsules returned by the patients. In the protocol, good compliers were defined as patients taking more than 80% of the prescribed treatment. Table 1 summarizes the incidence of death during the 5-year follow-up period, based on the treatment assigned and compliance status. Patients who left the trial before the end of the 5-year follow-up period were excluded.


Table 1. The compliance status and incidence of death during a 5-year follow-up period in the CDP trial.

In the clofibrate group, 708 patients were considered good compliers; 106 died during the follow-up period. There were 357 patients considered poor compliers; 88 died. Comparing the compliance status of the proportion of patients that died yields 106/708 – 88/357 = –9.68%. From this result, clofibrate seems to have been beneficial. However, when we make the same comparison for the placebo group, it yields 274/1813 – 249/882 = –13.12%. Surprisingly, we obtain the result that the placebo was more beneficial than clofibrate. However, nobody would interpret the result as being that the placebo had the effect of decreasing death.

Causal Inference in Randomized Trials with Noncompliance 317

independent from *X* given *R* and *Z*, where *Z* is a confounder or a set of confounders between *X* and *Y*. In Sections 3-5, we also require the instrumental variable (IV) assumption, which states that the potential outcome *YX*=*<sup>x</sup>* is not affected directly by the treatment assignment *R*; rather, *YX*=*<sup>x</sup>* is influenced only by the treatment actually received (Holland, 1986; Angrist et al., 1996). Thus, subjects' potential outcomes are independent of treatment assignment and are constant across the sub-populations of subjects assigned to different

ASSUMPTION 1: Instrumental variable (IV) E(*YX*=*<sup>x</sup>*|*R* = 2) = E(*YX*=*<sup>x</sup>*|*R* = 1). This assumption may hold in successfully blinded randomized trials, because subjects are not aware of their assigned treatments and so the assigned treatments do not affect the potential outcomes. However, this often may not hold in unblinded trials, in which subjects are aware of the assigned treatment and this knowledge may affect the potential outcomes, and needs to be critically evaluated. Assumption 1 is used in Sections 3-5, but is relaxed in

In this section and the next section, we discuss noncompliance by switching the treatment, which means that non-compliers in a sub-population assigned to treatment A receive treatment B and those assigned to treatment B receive treatment A. In this type of noncompliance, all subjects have the value *X* = 1 or 2 (and not *X* = 0) for both *R* = 1 and 2. Thus, *p*0|*<sup>r</sup>* = 0 and *p*1|*<sup>r</sup>* + *p*2|*<sup>r</sup>* = 1. The derivations of equations in this section are given in

In this section, we discuss how estimates from major analyses, such as ITT and PP, are biased. To do so, we introduce the following *R*-specific bias factors due to confounding

*α<sup>r</sup>* ≡ E(*YX*=2|*X* = 2, *R* = *r*) – E(*YX*=2|*X* = 1, *R* = *r*),

*β<sup>r</sup>* ≡ E(*YX*=1|*X* = 2, *R* = *r*) – E(*Y X*=1|*X* = 1, *R* = *r*), where *r* = 1, 2. *αr* and *βr* are confounding effects that would arise from *R*-stratified comparisons of those with *X* = 2 versus those with *X* = 1. When *αr* > 0 and *βr* > 0, E(*YX*=*<sup>x</sup>*|*X* = 2, *R* = *r*) > E(*YX*=*<sup>x</sup>*|*X* = 1, *R* = *r*), which means that the subjects who received the test treatment tend to have larger outcome values than those who received the control, leading to positive confounding. Conversely, when *αr* < 0 and *βr* < 0, E(*YX*=*<sup>x</sup>*|*X* = 2, *R* = *r*) < E(*YX*=*<sup>x</sup>*|*X* = 1, *R* = *r*), which means that the subjects who received the test treatment tend to have smaller outcome values than those who received the control, leading to negative

E(*YX*=2) = *E*2*<sup>r</sup>* – *αrp*1|*<sup>r</sup>*, (3.1)

 E(*YX*=1) = *E*1*<sup>r</sup>* + *βrp*2|*<sup>r</sup>*. (3.2) Using these equations, ITT ≡ E(*Y*|*R* = 2) – E(*Y*|*R* = 1) can be expressed by a function of ACE

treatment arms. The IV assumption is formalized as follows:

between *X* and *Y* (Brumback et al, 2004; Chiba et al., 2007):

confounding. No confounding occurs between *X* and *Y* when *αr* = *βr* = 0. Under Assumption 1, using *αr* and *βr*, E(*YX*=2) and E(*YX*=1) are expressed as:

Section 6.

Section 8.1.

**3. Biases of estimates** 

≡ E(*YX*=2) – E(*YX*=1) and bias factors:

Which subgroups to compare to estimate the treatment effect correctly is an important problem. From the viewpoint of treatment compliance, it is considered best to compare the proportion of deaths for the compliers in each group: 106/708 – 274/1813 = –0.14%. This comparison is called the per-protocol (PP) analysis. The PP analysis generally yields biased estimates of treatment effects, because whether patients comply with the assigned treatment is not randomized and several factors may affect it. This problem can be avoided by intention-to-treat (ITT) analysis, in which patients are analyzed according to the assigned treatment regardless of the treatment actually received (Fisher et al., 1990; Lee et al., 1991): 194/1065 – 523/2695 = –1.19%. The ITT estimate may represent the effect of the treatment intended, but generally does not represent the treatment effect itself (Schwartz & Lellouch, 1967; Sheiner & Rubin, 1995).

Noncompliance data may be obtained from actual clinical trials, as in the CDP trial. To estimate the treatment effect correctly from such data, we should consider the expected outcomes if all patients had received the test treatment and the control, and compare them. The effect yielded from such a comparison is called the average causal effect (ACE) (Robins & Tsiatis, 1991; Robins & Greenland, 1994). Several researchers have discussed methodology to estimate ACE (Pearl, 2000; Manski, 2003; Sato, 2006), but as yet, no standard methodology has been developed. Nevertheless, we can derive bounds on ACE using the deterministic causal model (e.g., Pearl, 1995; Cai et al., 2007; Chiba, 2009b). In this chapter, we discuss how estimates from major analyses, such as ITT and PP, are biased and present bounds on ACE under certain assumptions.

To achieve these objectives, this chapter is organized as follows. In Section 2, notation and definitions are provided. Sections 3 and 4 discuss noncompliance by switching the treatment, which, in contrast to the CDP trial, means that non-compliers in a sub-population assigned to treatment A receive treatment B and those assigned to treatment B receive treatment A. We discuss biases from major analyses such as ITT and PP in Section 3, and discuss the bounds on ACE in Section 4. Section 5 discusses noncompliance by receiving no treatment, as in the CDP trial. As in many publications, the instrumental variable (IV) assumption is used in these sections, but this assumption is relaxed in Section 6. Finally, Section 7 offers some concluding remarks. The derivations of equations and inequalities presented in this chapter are outlined in Section 8.
