A Tutorial on Interaction

2.1 Motivations for assessing interaction

There are a number of practical and theoretical considerations that motivate the study of interaction. One of the most prominent of these is that, in a number of settings, resources to implement interventions may be limited. It may not be possible to intervene on or treat an entire population. Resources may only be sufficient to treat a small fraction. If this is the case, then it may be important to identify the subgroups of individuals in which the intervention or treatment is likely to have the largest effect. As will be discussed below, methods for assessing additive interaction can help determine which subgroups would benefit most from treatment. Other more sophisticated methods can help identify groups of individuals, based on a large number of covariates, who would or would not benefit, or who would benefit to the greatest extent, from treatment. Even in settings in which resources are not limited and it is possible to intervene on everyone, it may be the case that a particular intervention is beneficial for some individuals and harmful for others. In such cases, it is very important to identify those groups for which treatment may be harmful and refrain from treating such persons. Techniques for assessing such so-called “qualitative” or “crossover” interactions are discussed in this tutorial are useful in this regard.

Another reason sometimes given for empirically assessing interaction is that it may provide insight into the mechanisms for the outcome. We will describe in this tutorial how it is possible to sometimes detect individuals for whom an outcome would occur if both exposures are present but would not occur if just one or the other were present. We will see that this more mechanistic notion of interaction is quite distinct from more statistically-based notions of interaction; we will see that in some cases we can gain insight into whether there might be a mechanism requiring two or more specific causes to operate and we will discuss the limits of such reasoning. Yet another reason sometimes given for studying interaction is that leveraging interactions that may be present may in fact help increase power in testing for the overall effect of an exposure on an outcome. In some settings, by jointly testing for a main effect and for an interaction simultaneously, it is possible to detect an overall effect when tests that ignore the interaction would not otherwise be able to detect the effect. It has been proposed that this may be especially important in the context of studying genetic variants when many variants are being tested and correction for such multiple testing reduces power, whereas allowing for the joint test may increase power to detect the effects.

As noted above, one of the motivations for studying interaction is to identify which subgroups would benefit most from intervention when resources are limited. However, in some settings, it may not be possible to intervene directly on the primary exposure of interest, and one might instead be interested in which other covariates could be intervened upon to eliminate much or most of the effect of the primary exposure of interest. In these cases, methods for attributing effects to interactions, discussed in the latter part of the tutorial, can be useful in assessing this and identifying the most relevant covariates for intervention. Finally, sometimes interactions are modeled not with any specific scientific or policy goal in mind concerning interactions per se, but simply because the statistical model fits the data better when the model includes the additional flexibility allowed by an interaction term. These various motivations for studying interaction are distinct and, as we will see throughout, when studying interaction it is important to clearly understand what the goal of the analysis is.

2.2 Measures of interaction and scale of interaction

As a motivating example, consider data presented in Hilt et al. (1986) concerning the effect of smoking on lung cancer and how this varied by previous exposure to asbestos. The risk of lung cancer comparing smokers and non-smokers varied by asbestos exposure as presented in Table 1.

It seems as though lung cancer risk is much higher when both smoking and asbestos exposure are present together. This is an example of what we might call an interaction.

Let D denote a binary outcome. Let G and E denote two binary exposures of interest. These might be a genetic factor and an environmental factor, respectively, but our discussion will not be restricted to gene–environment interaction and G and E could represent any two factors; later in the tutorial we will also discuss interaction when the factors are not binary, but much of the discussion here generalizes in a straightforward manner. Let pge=P(D=1|G=g,E=e) be the probability of the outcome when G is value g and E is value e. A natural way to assess interaction is to measure the extent to which the effect of the two factors together exceeds the effect of each considered individually (cf. Rothman, 1986; Szklo and Nieto, 2007). This could be measured by:

Here (p11−p00) would be interpreted as the effect of both factors together compared to the reference category of both factors absent. The expressions (p10−p00) and (p01−p00) would be the effects of the first factor alone and the second factor alone, respectively. We would then consider the contrast between the effects of both factors together versus the sum of each considered separately. If this difference were non-zero we might say that there was interaction on the difference scale. For now, we will assume that the probabilities of the outcome under different exposure combinations correspond to the actual effects of the exposures on the outcome; we will consider issues of confounding and covariate adjustment in interaction analyses further below.

The measure in eq. [1] is sometimes referred to as a measure of interaction on the additive scale. The measure in eq. [1] can be rewritten as:

If p11−p10−p01+p00>0, the interaction is sometimes said to be positive or “super-additive.” If p11−p10−p01+p00<0, the interaction is said to be negative or “sub-additive”.

For the data in Table 1, we have

We would have evidence here of positive or “super-additive” interaction.

Sometimes, instead of using risk differences to measure effects, one might use risk ratios or odds ratios. For example, we could define the risk ratio effect measures as:

,

,

.A measure of interaction on the multiplicative scale for risk ratios could then be taken as:

This quantity measures the extent to which, on the risk ratio scale, the effect of both exposures together exceeds the product of the effects of the two exposures considered separately. If RR11/(RR10RR01)>1, the multiplicative interaction is said to be positive. If RR11/(RR10RR01)<1, the multiplicative interaction is said to be negative. Note that we compare the measure RR11/(RR10RR01) to 1 rather than to 0 here since RR11/(RR10RR01) is a ratio. If the ratio is 1, then the effect of both exposures together is equal to the product of the effect of the two exposures considered separately, that is, there is no interaction on the multiplicative scale for risk ratios. This measure of multiplicative interaction can also be rewritten as RR11RR10RR01=p11p01/p10p00, i.e. as the ratio of (i) the relative risk for G when E=1 versus (ii) the relative risk for G when E=0. Likewise, it can be written as RR11RR10RR01=p11p10/p01p00, i.e. as the ratio of (i) the relative risk for E when G=1 versus (ii) the relative risk for E when G=0.

Using the data in Table 1, we have that the measure of multiplicative interaction is given by:

We would have evidence here of negative multiplicative interaction.

This example also demonstrates that whether an interaction is positive or negative may depend on the scale. We may have a positive interaction on the additive scale but a negative interaction on a multiplicative scale. Said another way, the effect of both exposures together on the risk difference scale may exceed the sum of the effects on the risk difference scale of each considered separately, while it also being the case that the risk ratio for both exposures together is less than the product of the effects of the two exposures considered separately.

Likewise, interaction may be present on one scale but absent on another. Consider the data in Table 2.

Here there is no additive interaction since p11−p10−p01+p00=0.10−0.07−0.05+0.02=0 but there is a negative multiplicative interaction since RR11/(RR10RR01)=(0.10/0.02)/{(0.07/0.02)(0.05/0.02)}=5/(3.5×2.5)=0.57<1. Likewise in other settings we might have additive interaction but no multiplicative interaction. Consider the data in Table 3.

Here the additive interaction is positive since p11−p10−p01+p00=0.10−0.04−0.05+0.02=0.03>0, but there is no multiplicative interaction since RR11/(RR10RR01)=(0.10/0.02)/{(0.04/0.02)(0.05/0.02)}=5/(2×2.5)=1. In fact it can be shown (cf. Greenland et al., 2008) that if both of the two exposures have an effect on the outcome, then the absence of interaction on the additive scale implies the presence of multiplicative interaction for relative risks and likewise, the absence of multiplicative interaction for relative risks implies the presence of additive interaction. In other words, if both of the two exposures have an effect on the outcome, then there must be interaction on some scale. This raises the question of why interaction is of interest and which scale is to be preferred. It also makes clear that just to say that there is an interaction on some scale is relatively uninteresting; all it means is that both exposures have some effect on the outcome. Once again, when undertaking interaction analyses it is important to clarify what the goal or the motivation for the analysis is and choose a measure of interaction accordingly. In a subsequent section, we will turn to the arguments for and interpretation of additive versus multiplicative interaction. In general, however, either the presence or the absence of additive or multiplicative interaction may be of interest, and so it may be good practice to evaluate both additive and multiplicative interactions.

One reason why additive interaction is important to assess (rather than only relying on multiplicative interaction measures) is that it is the more relevant public health measure (Blot and Day, 1979; Saracci, 1980; Rothman et al., 1980; Greenland et al., 2008). Consider again the outcome probabilities in Table 3. Suppose that the outcome probabilities represent the probability of a disease being cured for a drug (E) stratified by genotype status (G). The effect of E on the risk difference scale among those with G=0 is 0.05−0.02=0.03; while the effect of E among those with G=1 is 0.10−0.04=0.06. If we had only 100 doses of the drug and we had to decide which group to treat, we could cure three additional persons if we used all of the drug supply among those with G=0, but we could cure six additional persons if we used all of the drug supply among those with G=1. All other things being equal, we would clearly want to give the drug supply to those with G=1. The additive interaction measure, p11−p10−p01+p00=0.03>0, allows us to see this. The multiplicative interaction measure, RR11/(RR10RR01)=1, does not.

In fact, the multiplicative scale can indicate the wrong subgroup to treat. Suppose in Table 3 we replace the final probability of cure 0.10 with 0.09. Then the effect on the difference scale of E among those with G=0 is 0.05−0.02=0.03; the effect of E among those with G=1 is 0.09−0.04=0.05. Thus, on the difference scale, the effect size is larger for the G=1 subgroup, indicating this is the subgroup we would like to treat if resources are limited. However, on the risk ratio scale, the effect for those with G=0 is 0.05/0.02=2.5 and for those with G=1 it is 0.09/0.04=2.25; the risk ratio effect size is larger for the G=0 subgroup; however, this is not the subgroup we would want to allocate limited resources to. If we had only 100 doses of the drug, we could cure three additional persons if we used all of the drug supply among those with G=0, but we could cure five additional persons if we used all of the drug supply among those with G=1. All other things being equal, we would clearly want to give the drug supply to those with G=1. The issue with the multiplicative scale here is that the baseline risk is different in the two subgroups, and thus the risk ratio is operating on different baseline risks.

The possibility of positive additive interaction but negative or null multiplicative interaction is not simply a theoretical possibility. This was precisely the situation with the lung cancer data in Table 1 where we had a positive additive interaction, but a negative multiplicative interaction. It was likewise the case in analyses of the joint effects of Helicobacter pylori and use of NSAIDs in causing peptic ulcer (Kuyvenhoven et al., 1999) with slightly positive additive interaction but negative multiplicative interaction. Similarly, in analyses of interaction between factor V Leiden mutation and oral contraceptive use in causing venous thrombosis, the multiplicative interaction was found to be close to null, but there was a positive additive interaction (Vandenbroucke et al., 1994). Using the multiplicative interaction results in any of these cases to determine which subgroups to prioritize intervention would have given the wrong conclusion. For example, from the data in Table 1 more lives would be saved by removing asbestos from homes of smokers first; the risk ratios give the opposite conclusion. Indeed dismissing the importance of one factor in assessing the effects of another because of the absence of multiplicative interaction can be quite dangerous: the null multiplicative interaction between factor V Leiden mutation and oral contraceptive use may lead to false reassurances that “it does not matter” whether one carries the mutation or not for the decision to start using oral contraceptives; whereas, in fact, because those with the factor V Leiden mutation have a roughly seven times higher baseline risk than those without the mutation (Vandenbroucke et al., 1994), the “constant risk ratio” for oral contraceptive use results in a much higher increase in absolute risk for those with the factor V Leiden mutation than those without.

More generally, p11−p10−p01+p00>0 implies the public health consequence of an intervention on E would be larger in the G=1 group, while p11−p10−p01+p00<0 implies the public health consequence of an intervention on E would be larger in the G=0 group. Thus, while it may be of interest to assess multiplicative interaction, additive interaction should also in general be examined, if for no other reason than to assess public health relevance.

In some case–control study designs, only the odds ratio can be evaluated and thus effect measures and interaction measures are evaluated on an odds ratio scale. The effects for each of the exposures considered separately and both considered together on the odds ratio scale are defined respectively by:

,

,

A measure of interaction on the multiplicative scale for odds ratio could then be taken as:

This quantity measures the extent to which, on the odds ratio scale, the effect of both exposures together exceeds the product of the effects of the two exposures considered separately. If OR11/(OR10OR01)>1, the multiplicative interaction is said to be positive. If OR11/(OR10OR01)<1, the interaction is said to be negative. For the data in Table 1, we have

The measure of multiplicative interaction on the odds ratio scale is negative. The measure is very close to what was obtained for the multiplicative interaction on the risk ratio scale, i.e. 0.78.

In general, measures of multiplicative interaction on the odds ratio and risk ratio scales will be very close to one another whenever the outcome is rare. When the outcome is rare, both (1−pge) and (1−p00) will be close to 1 and thus the odds ratios approximate risk ratios since

Odds ratios will also equal risk ratios (even when the outcome is common) in certain case–control designs in which the controls are selected from the entirety of the underlying population rather than just from the non-cases (cf., e.g. Knol et al., 2008, for further review and discussion of this point).

We may also be interested in assessing additive interaction from data when only relative risks are available or reported. Although we may not be able to estimate the additive interaction in eq. [2], i.e. p11−p10−p01+p00, directly, we can still proceed as follows. If we divide eq. [2] by p00 we obtain the following:

This quantity is sometimes referred to as the “relative excess risk due to interaction” or RERI (Rothman, 1986). It is also sometimes referred to as the “interaction contrast ratio” or ICR (Greenland et al., 2008). This gives us something similar to additive interaction but using risk ratios rather than risks. Subsequently, we will refer to this quantity in eq. [5] as RERIRR. We have that RERIRR>0 if and only if for the additive interaction in eq. [2], p11−p10−p01+p00>0; likewise RERIRR<0 if and only if p11−p10−p01+p00<0; and RERIRR=0 if and only if p11−p10−p01+p00=0. Thus, we can assess whether additive interaction is positive, negative, or zero using risk ratios and RERIRR. It should be noted that although RERIRR gives the direction (positive, negative, or zero) of the additive interaction, we cannot in general use RERIRR to make statements about the relative magnitude of the underlying additive interaction for risks, p11−p10−p01+p00, unless we know p00. We may have RERIRR larger in one of two subpopulations, but the additive interaction for risks, p11−p10−p01+p00, may be larger in the other; this is because the baseline risks, p00, may differ and RERIRR depends on the baseline risk (Skrondal, 2003).^[1] However, again, only the direction, rather than the magnitude, of RERIRR is needed to draw conclusions about the public health relevance of interaction. If we are trying to decide which subgroup of G to target for an intervention when resources are limited, RERIRR>0 implies the public health consequences of an intervention on E would be larger in the G=1 group, while RERIRR<0 implies the public health consequences of an intervention on E would be larger in the G=0 group.

A few other measures of additive interaction using data from risk ratios or odds ratios are sometimes employed. The so-called synergy index (Rothman, 1986) is defined as:

It measures the extent to which the risk ratio for both exposures together exceeds 1, and whether this is greater than the sum of the extent to which each of the risk ratios considered separately each exceed 1. Suppose the denominator of S is positive, then if S>1 then we will have RERIRR>0 and thus p11−p10−p01+p00>0; and if S<1 then we will have RERIRR<0 and thus p11−p10−p01+p00<0. Thus, the synergy index can likewise be used to assess additive interaction. The interpretation of the synergy index becomes difficult in settings in which one or both of the exposures is preventive rather than causative so that the denominator of S is negative (Knol et al., 2011).^[2] This issue does not arise with RERIRR because the denominator of RERIRR is never negative. The issue can be resolved with the synergy index S by recoding the exposures so that neither is preventive in the absence of the other (Knol et al., 2011). Another measure of additive interaction that is sometimes used is called the attributable proportion and is defined as:

and essentially measures the proportion of the risk in the doubly exposed group that is due to the interaction itself. The attributable proportion is essentially a derivative measure of the relative excess risk due to interaction: AP>0 if and only if RERIRR>0; and AP<0 if and only if RERIRR<0. A variant on the attributable proportion may also be potentially of interest. The attributable proportion measured above, AP=RERIRRRR11=RR11−RR10−RR01+1RR11=p11−p10−p01+p00p11, essentially measures the proportion of risk in the doubly exposed group that is due to interaction. Alternatively, we might consider the proportion of the joint effects of both exposures together that is due to interaction (Rothman, 1986; VanderWeele, 2013). This measure is given by AP∗=RERIRRRR11−1=RR11−RR10−RR01+1RR11−1=p11−p10−p01+p00p11−p00. Its properties will be considered later in the tutorial in the section on attributing effects to interactions.

All of these measures can be used in cohort studies, but these measures are also of interest and can be employed in case–control studies as well. Suppose that we only have estimates for odds ratios but that the outcome is rare (or that the controls are selected from the entirety of the underlying population rather than just from the non-cases cf. Knol et al., 2008) so that odds ratios approximate risk ratios. We could then replace each of the risk ratios in RERIRR, the synergy index S, or the attributable proportion measures, with odds ratios to obtain approximations to each of these measures of additive interaction. For example, for the relative excess risk due to interaction, we can define RERIOR=OR11−OR10−OR01+1, which is the odds ratio analog of RERIRR. If the outcome is rare then we have that

Thus, when odds ratio approximate risk ratios, we can assess additive interaction, at least approximately, even if only estimates of odds ratios are available from case–control study designs. Note that for this argument to apply using the assumption of a rare outcome (10% is often used as a threshold in practice), the outcome must be rare in each stratum defined by the two exposures. Sampling controls for the entire underlying population rather than only the non-cases removes the need for this rare outcome assumption.

As an example, Figueiredo et al. (2004) studied the effects of XRCC3-T241M polymorphisms and alcohol consumption on breast cancer risk using a case–control study design. The genetic risk factor was considered the M/M genotype versus a reference of the T/T or T/M genotype. They obtained the odds ratio in Table 4 from their case–control study.

Although we cannot assess additive interaction directly using risks, p11−p10−p01+p00, from the odds ratios in Table 4, we can still estimate

and so we would have evidence of positive additive interaction. Breast cancer is a relatively rare outcome, and so odds ratios will closely approximate risk ratios in this study. Likewise, we could calculate the synergy index S=RR11−1(RR10−1)+(RR01−1)=3.30>1, again indicating positive additive interaction. And we can calculate the proportion of risk in the doubly exposed group attributable to interaction, AP=RR11−RR10−RR01+1RR11=36.4% or the proportion of the joint effects of both exposures attributable to interaction, AP∗=RR11−RR10−RR01+1RR11−1=69.7%.

2.3 Statistical interactions and statistical inference

In practice, interactions are often evaluated by using statistical models by including a product term for the two exposures in the model. A statistical model on the linear scale accommodating interaction might take the form:

It can be verified under this model that α0=p00, α1=p10−p00, α2=p01−p00, and α3=p11−p10−p01+p00. The coefficient α3 is thus equal to our measure of additive interaction based on risks; for this reason, α3 is sometimes referred to as a statistical interaction on the additive scale.

Similarly, one might use a log-linear model for risk ratios, including a product term:

Here we have that eβ0=p00, eβ1=RR10, eβ2=RR01, and eβ3=RR11/(RR10RR01). The so-called “main effects”, β1 and β2, when exponentiated, simply give the risk ratios for each of the two exposures when each is considered alone. The coefficient β3, when exponentiated, gives our measure for multiplicative interaction for risk ratios, RR11/(RR10RR01). The coefficient β3 is thus often referred to as a statistical interaction for a log-linear model. Likewise, one might use a logistic model for odds ratios, including a product term:

Here we have that eγ0=p00/(1−p00), eγ1=OR10, eγ2=OR01, and eγ3=OR11/(OR10OR01). The main effects, γ1 and γ2, when exponentiated, simply give the odds ratios for each of the two exposures. The coefficient γ3, when exponentiated, gives our measure for multiplicative interaction for odds ratios, OR11/(OR10OR01). Thus, γ3 is referred to as a statistical interaction for a logistic model. The equality eγ0=p00/(1−p00) will only hold with cohort data. However, all the other equalities, eγ1=OR10, eγ2=OR01, and eγ3=OR11/(OR10OR01), will hold for both cohort data and case–control data. We can thus assess both of the main effects of the exposure and the multiplicative interaction between the exposures on an odds ratio scale using case–control data.

When the outcome and both exposures are binary, and no further covariates are included, it is straightforward to fit these models to the data using standard software. The estimate and confidence intervals obtained by maximum likelihood estimation and given by such software for α3 will constitute an estimate and confidence interval for the additive interaction p11−p10−p01+p00. The estimate and confidence intervals obtained by maximum likelihood estimation and given by such software for β3 and γ3, when exponentiated, will constitute an estimate and confidence interval for the multiplicative interaction on the risk ratio and odds ratio scales, respectively. Statistical inference for interaction is thus straightforward in these cases.

Often we may want to control for other covariates in models [6]–[8]. For example, we may want to fit the following analogous models which include an additional vector of covariates, C:

,

,

Unfortunately, the linear and log-linear models, when fit to data, will often run into convergence problems in the maximum likelihood algorithms used to fit the models, especially when there are continuous covariates in C, because the models do not ensure that the predicted probabilities lie between 0 and 1. The logistic model with covariates does not suffer from this problem. For this reason, the most common approach to assessing interaction in practice has become fitting the logistic model with covariates and assessing the estimate and confidence interval for the product term coefficient, γ3, in this model. This approach is also popular because it can be implemented in a straightforward way with case–control data as well. The coefficient, γ3, is an important and useful measure of interaction and proceeding with this strategy is recommended.

However, as discussed throughout this tutorial, it is also recommended that investigators assess additive interaction as well. This can be more challenging when covariates are in the model. Additional strategies to fit linear and log-linear models with covariates using data from cohort studies have been described elsewhere (cf. Yelland et al., 2011; Knol et al., 2012, for overviews of several different methods). In the next section, however, we will describe what has now become a fairly standard approach (Hosmer and Lemeshow, 1992) to estimating additive interaction, with covariate control, which consists of using a logistic regression with additional covariates and transforming the parameter estimates to obtain estimates and confidence intervals for the relative excess risk due to interaction (RERI).

2.4 Inference for additive interaction

Suppose the following model is fit to the data:

We then have that

Thus, we can estimate a measure of additive interaction, RERIOR, using the parameters of a logistic regression. This approach has the advantage that the logistic regression in eq. [9] can more easily be fit to data when there are continuous covariates than the corresponding linear or log-linear models for binary outcomes given in the previous section. This approach with logistic regression also has the advantage that it can be employed even with case–control data. Even with cohort data, if the outcome is rare, this approach to additive interaction using RERIOR can often be helpful because the logistic regression model often fits data quite well and has fewer convergence issues than a linear or log-linear model for risk, as discussed above. The logistic regression model has the interesting implication that if the model is correctly specified so that the log odds are linear in the covariates C, then the RERIOR measure will also be constant across strata of the covariates. This approach to RERIOR, as other modeling approaches, presupposes that the statistical model is correctly specified. We discuss below other modeling approaches for additive interaction that make different modeling assumptions.

Standard errors for RERIOR, as estimated above, can be obtained using the delta method (Hosmer and Lemeshow, 1992). Software options are now available to estimate these standard errors (e.g. Lundberg et al., 1996; Andersson et al., 2005).^[3] In the Appendix, we provide some simple SAS code to estimate RERIOR and its standard error using the delta method. We likewise describe how this can be done in Stata (cf. Ai and Norton, 2003; Norton et al., 2004). Finally, as an online supplement to this tutorial, we have provided an Excel spreadsheet that can be used in conjunction with standard output from logistic regression (output on parameter estimates and either the covariance or correlation estimates) using any software package. The current Excel spreadsheet offers somewhat more flexibility than previous versions of the spreadsheet in allowing for confidence intervals of any percentile.

The approach described above works well if the outcome is rare so that RERIOR approximates RERIRR. If the outcome is common, RERIOR may not be an adequate measure of additive interaction. In such cases, for cohort data, one could estimate RERIRR by replacing the logistic model in eq. [9] with a log-linear model, though such log-linear models with continuous covariates C may not always converge; likewise an approach for risk ratios using modified Poisson, rather than logistic regression, has also been proposed that can be used with a common outcome (Zou, 2008). Alternatively, with cohort data with a common outcome, one may use a weighting approach to estimating additive interaction (VanderWeele et al., 2010). This approach models the relationship between the exposures and the covariates, rather than between the outcome and the covariates.

Our discussion thus far has focused on binary exposures. A similar approach can be used with categorical, ordinal, or continuous exposures. The logistic regression model above in eq. [9] could be fit to the data if the two exposures G and E were ordinal or continuous. However, when additive interaction is carried out for ordinal or continuous exposures using this approach based on logistic regression, two things must be kept in mind, one analytical and one interpretative. First analytically, for ordinal and continuous exposures, it is important to consider the magnitude of the change in the exposures for which one is examining interaction. If one is considering a change for the value of G from g0 to g1 and a value of E from e0 to e1 then instead of using eγ1+γ2+γ3−eγ1−eγ2+1 as an estimate of RERIOR one uses

This needs to be taken into account when using the software and Excel spreadsheets, so that estimates and covariance matrices are multiplied by the appropriate factors. This is described in more detail in the Appendix. Similar expressions could be given using categorical exposures: under any specific statistical model and for any two levels of each of the two exposures, one simply calculates the three relative risks comparing the various exposure combinations to the reference group and one subtracts from the risk ratio of the doubly exposed group, the two risk ratios for each of the singly exposed groups and adds 1. The second, more interpretative point, when ordinal, continuous, or categorical exposures are being employed, is that it is important to keep in mind that the RERIOR measure (or the analogous RERIRR measure) does vary according to the levels being compared and can vary in sign as well. The additive interaction measure for a change in E from 10 to 20 and in G from 0 to 1 may be different than the additive interaction measure for a change in E from 20 to 30 and in G from 0 to 1, but again as noted above, the RERIOR measure should be interpreted as giving the direction of additive interaction (positive, negative, or zero) and its relative magnitude does not necessarily correspond to the relative magnitude of the additive interaction for absolute risks. See also Knol et al. (2007) for further discussion. SAS and Stata code are given in the Appendix.

2.5 Additive versus multiplicative interaction

The fact that interaction can be assessed on different scales and that interaction is scale dependent raises the question on which scale interaction should be assessed: additive or multiplicative or some other. The view of this tutorial is that it is almost always best to present both additive and multiplicative measures of interaction (Botto and Khoury, 2001; Vandenbroucke et al., 2007; Knol and VanderWeele, 2012). In practice, measures of multiplicative interaction, using logistic regression, are most frequently reported. This is very likely simply done because of convenience, rather than because careful thought has been given to which measure is to be preferred. Standard software using logistic regression will automatically give an estimate and confidence interval for multiplicative interaction. As noted in the previous section, additional work is required in most current software packages to obtain measures of additive interaction, and for this reason it is not often done. In a recent review of a random sample of 25 cohort and 50 case–control studies from the five most highly ranked epidemiological journals, Knol et al. (2009) noted that although 61% of the studies included at least as secondary analyses an assessment of effect modification or interaction, only one reported a measure of additive interaction. In our view, it is in general a mistake to not report additive interaction. As noted above and as discussed further below, additive interaction is always relevant for assessing the public health significance of an interaction. Although we believe both additive and multiplicative interactions should in general be reported, we nonetheless review some of the reasons that have been put forward for using one scale versus the other.

The difference scale is useful for assessing the public health importance of interventions and the public health significance of interaction (Blot and Day, 1979; Saracci, 1980; Rothman et al., 1980; Greenland et al., 2008). As noted above, if the effect of an intervention is larger on the difference scale in one subgroup versus another, then this indicates that there would be larger numbers for whom the disease was prevented/cured in giving a hundred individuals in the first subgroup treatment versus giving a hundred individuals in the second subgroup treatment. Such information is useful for targeting subpopulations for which the intervention is most effective. This will be relevant whenever resources are constrained and thus relevant also for cost-effectiveness (Greenland, 2009). As discussed above, the additive, not the multiplicative, scale gives this information. A second reason sometimes given for using additive interaction is that it more closely corresponds to tests for mechanistic interaction, rather than merely statistical interaction (Greenland et al., 2008; VanderWeele and Robins, 2007, 2008; VanderWeele, 2010a, 2010b). As discussed further below, tests for additive interaction can sometimes be used to detect synergism in Rothman’s (1976) sufficient cause framework. Conceived of another way, assessing additive interaction can sometimes be used to assess whether there are persons for whom the outcome would occur if both exposures were present but not if only one or the other of the exposures were present. As discussed below, this ends up being a different, and in many cases stronger, notion of interaction than merely a statistical interaction. We return to this point in later sections. Finally, as also discussed further below, tests for additive interaction are sometimes more powerful than tests for multiplicative interaction and thus for the purposes of discovery and detection, the additive scale may be preferred as well.

Several reasons are also often put forward for using the multiplicative scale. First, as noted above, it is easier to fit multiplicative models (such as logistic regression), and the multiplicative scale is the most natural scale on which to assess interaction for such models; moreover, when using such models, measures of multiplicative interaction are readily obtained from standard software. Second, it is sometimes claimed that there is in general less heterogeneity on the multiplicative scale. Studies of meta-analyses have suggested that in terms of statistical significance, the risk ratio and odds ratio are less heterogeneous than the risk difference (Engels et al., 2000; Sterne and Egger, 2001; Deeks and Altman, 2003).^[4] However, it is not entirely clear the extent to which this is simply due to difference in power across the different scales or whether there is genuinely less heterogeneity. Nevertheless, if it is indeed the case that the multiplicative scales (odds ratio or risk ratio) are “less heterogeneous”, and this indicates something about the underlying biology as to how effects typically operate (see comments on the “Limits of Biologic Inference” below), then detecting an interaction on a multiplicative scale may be of greater import than detecting interaction on the additive scale. A third reason sometimes given for using the multiplicative scale for overall effects (but also potentially applicable to interaction), stated in some epidemiology textbooks, is that the relative effect measures are better suited to “assessing causality”. According to Poole (2010), this notion can be traced back to a paper by Cornfield et al. (1959) showing that smoking was strongly related to lung cancer but not to other diseases on a relative risk scale, while smoking seemed similarly related to lung cancer and also to other diseases on an absolute risk scale. Because specificity of effect was seen as a criterion of causality (Hill, 1965), the relative risk scale was seen as superior over the absolute risk scale in assessing causality. As noted by Poole (2010), whether the relative or absolute measure is more useful for “assessing causality” will, however, vary by setting. In some cases, such as that considered by Cornfield et al. (1959), the multiplicative scale may indeed prove to be more useful, and it might be thought that this general argument then is also relevant to interaction.

Arguments can be given in favor of each of the two scales. However, nothing prohibits investigators from reporting measures of interaction on both additive and multiplicative scales and, in most settings, we think this approach is the best because both can be informative (Botto and Khoury, 2001; Vandenbroucke et al., 2007; Knol and VanderWeele, 2012). The presence or absence of interaction on either scale may be of interest. However, as noted above, provided both exposures have an effect on the outcome, there will always be interaction on at least one scale.^[5] The only way there can be no interaction on any scale is for one of the two exposures to have no effect on the outcome at all. Thus, the fact that interaction is present on some scale really is not of much interest; provided both exposures have an effect on the outcome, such interaction on some scale will always be present. This brings us back to the point that was made at the beginning of the tutorial, that, when studying interaction, it is important to clearly understand what the goal of the analysis is: What is it that we are trying to learn? What scientific or policy question are we trying to answer and how does an interaction analysis help us? We have seen above already that interaction on the additive scale gives insight into which subgroups are best to treat. We will see below that interaction on the additive scale can also sometimes give insight into more mechanistic forms of interaction. As also discussed below the absence of interaction on either the additive or the multiplicative scale may also give some clues (though rarely definitive evidence) as to the underlying biology; likewise we will see that the presence of positive multiplicative interaction may give some clues as to mechanisms. But it is always important to clarify what the goal of the analysis is and what we are trying to learn. Again, the fact that there is interaction on some scale is otherwise nothing more than acknowledging that both exposures have some effect.

2.6 Confounding and the interpretation of interaction

Thus far, we have considered measures of interaction using risk differences, risk ratios, and odds ratios. In general, however, we want to know whether our effect estimates correspond to causal effects rather than mere associations. In observational studies, we thus attempt to control for confounding. Analytically, this is often done through regression adjustment for other covariates. In interaction analyses, we have two exposures and thus potentially two sets of confounding factors to consider. The causal interpretation of interaction measures depends on whether control has been made for one or both sets of confounding factors, or neither.

Suppose we have made control for one set of confounding factors, those for the relationship between our primary exposure of interest and the outcome, but that we have possibly not controlled for confounding of the relationship between the secondary factor defining subgroups and the outcome. We would in this case still be able to obtain valid estimates of the effect of the primary exposure within strata defined by our secondary factor. For example, suppose we found substantial interaction between a drug and hair color when examining some health outcome. If we had controlled for the confounding factors for the drug–outcome relationship, or if the drug were randomized, we could interpret our interaction measure as a measure of heterogeneity concerning how the actual causal effect of the drug varied across subgroups defined by hair color. If we found that the effect of our primary exposure varied by strata defined by the secondary factor in this way, then we might call this “effect heterogeneity” or “effect modification.” This might be useful, for example, in decisions about which subpopulations to target in order to maximize the effect of interventions. Provided we have controlled for confounding of the relationship between the primary exposure and the outcome, these estimates of effect modification or effect heterogeneity could be useful even if we have not controlled for confounding of the relationship between the secondary factor and the outcome. What we would not know, however, is whether the effect heterogeneity is due to the secondary factor itself, or something else associated with it. If we have not controlled for confounding for the secondary factor, the secondary factor itself may simply be serving as a proxy for something that is causally relevant for the outcome (VanderWeele and Robins, 2007b). For example, if we found that the effect of the drug varied by strata defined by hair color, this may simply be due to the fact that hair color is associated with genotype and it is this that is causally relevant for modifying the effect of the drug on the outcome. If we were simply to dye someone’s hair, this would not change the effect of the drug.

If we are interested principally in assessing the effect of the primary exposure within subgroups defined by a secondary factor then simply controlling for confounding for the relationship between the primary exposure and the outcome is sufficient. However, if we want to intervene on the secondary factor in order to change the effect of the primary exposure then we need to control for confounding of the relationships of both factors with the outcome. When we control for confounding for both factors we might refer to this as “causal interaction” in distinction from mere “effect heterogeneity” mentioned above (VanderWeele, 2009a).

As another example, VanderWeele and Knol (2011) considered a randomized trial for a housing intervention program for homeless adults to reduce the number of hospitalizations. Suppose that the effect of the housing program was examined within strata defined by whether the participants had at least part-time employment. Here, the housing program is randomized, but employment status is not. If it were found that the housing intervention had a larger effect for those with part-time employment than for those without, this could be used as a valid estimate for the effect of the intervention within these different subgroups and could be useful in subsequently targeting the intervention toward the subgroups for which it would be most effective. By randomization, we have controlled for confounding for the housing intervention, but we have not necessarily controlled for confounding for employment status. Thus, while we could get valid estimates of effects of the housing intervention within strata defined by employment status, we could not draw conclusions on what would happen if we intervened on employment status as well to try to improve the effect of the intervention. Again, employment status has not been randomized. Employment status may, for instance, be serving as a proxy for mental health, and it may be that mental health is in fact what is relevant in altering the effects of the intervention. It is possible that if we intervened on employment status, without changing mental health, then this would not alter at all the effect of the housing intervention. We would only be able to assess what the effect of interventions on employment status in altering the effect of the housing intervention would be if we had controlled for confounding of the relationship between the factor defining subgroups, namely employment status, and the outcome.

In summary, if we are interested in identifying which subpopulations it is best to target with a particular intervention, then assessing effect heterogeneity is fine and only the confounding factors of the relation between exposure and outcome need be considered (though even here it is sometimes argued control for other factors can help with external validity and extrapolation to other settings). If we are interested in potentially intervening on the secondary factor to change the effects of the primary intervention (or if we are interested in assessing mechanistic interaction, described below), then we want measures of causal interaction and we would need to control for confounding for the relationships between both factors and the outcome.

In practice, typically a regression model is simply fit to the data, regressing the outcome on the two exposures, a product term, and possibly other covariates. However, whether the regression coefficient for the product term can be interpreted as a measure of effect heterogeneity or causal interaction or both or neither depends on what confounding factors have been controlled for. For effect heterogeneity, we only have one set of confounding factors to consider, just those for the relationship between the primary exposure and the outcome. For causal interaction, we have two sets of confounding factors to consider, those for the primary exposure and the outcome and those for the secondary factor and the outcome. Epidemiologists are careful to control for confounding and think carefully about confounding in observational studies for overall causal effects. However, too often issues of confounding have been neglected in interaction analyses. Careful thought needs to be given to interaction analyses in interpreting associations as causal and in distinguishing between whether attempt is being made to control for one or both sets of confounding factors; and which of “effect heterogeneity” (also sometimes called “effect modification”) or “causal interaction” is of interest will depend upon the context.^[6]

The terms “interaction” and “effect modification” in practice are often used interchangeably. In some sense, what we have called “effect modification” is still a type of interaction analysis; and what we have called “causal interaction” could almost be viewed as “effect modification” by intervening on a secondary variable (VanderWeele, 2009a, 2010c). There is some ambiguity in terminology and it would be difficult to insist on a particular set of rules for terminology. However, even if the terms themselves are used interchangeably, it is important to keep in mind that there are still two distinct concepts present. The distinction again has to do with whether one or two potential interventions are in view. Failure to take the distinction into account could lead to incorrect policy recommendations. In writing papers, researchers can make clear which of the two concepts is in view (without having to adopt a strict terminological stance) by clarifying, in a Methods section, whether confounding control is intended for one or both exposures, and by commenting, in a Discussion section, whether interventions on one or both exposures are being considered when interpreting the implications of the results.

2.7 Presenting interaction analyses

Careful thought should be given to the presentation of interaction analyses. Very often when interaction or effect modification is of interest, effect measures are presented for each stratum separately using separate reference groups. Suppose, for example, we had data as in Table 1 and that effect measures were computed on the risk ratio scale. We let E=1 denote asbestos exposure and E=0 the absence of asbestos exposure and we let G=1 denote smoking and G=0 non-smoking. It is not uncommon for papers to present, e.g. the (adjusted) risk ratio effect measures for say the exposure E separately across strata of the other factor G. For example, the effect measures might be presented as in Table 5.

While this information can be useful to see that the risk ratio in the non-smoking (G=0) stratum is larger than the risk ratio in the smoking (G=1) stratum, and for calculating multiplicative interaction: 4.74/6.09=0.78 as above, there are several other comparisons for which Table 5 is uninformative. For example, by presenting the analyses with separate reference groups (for each of the G=0 and G=1 strata), we will not know from such a presentation whether the (G=0,E=1) subgroup or the (G=1,E=0) subgroup is at higher risk for the outcome. In fact, simply from the information in Table 5, we would not know whether the (G=1,E=1) subgroup or the (G=0,E=1) subgroup is at higher risk for the outcome, or whether the (G=1,E=0) subgroup or the (G=0,E=0) subgroup is at higher risk for the outcome. Nor do we know from Table 5 what the sign is for measures of additive interaction. Because of these reasons current guidelines (Vandenbroucke et al., 2007; Knol and VanderWeele, 2012) recommend that interaction and effect modification analyses be presented with a single common reference group, say the (G=0,E=0) subgroup, or that the original data be presented (Botto and Khoury, 2001). If risk ratios with a common reference group were used for the data in Table 1, the effects could then be presented in Table 6.

From the information presented in Table 6, which uses a common reference group, we would know that the ordering of risk across G×E subgroups was (G=0,E=0), then (G=0,E=1), then (G=1,E=0), and then (G=1,E=1). We could still calculate the individual risk ratios for E in the different strata of G as: 6.09/1=6.09 for G=0 and 40.91/8.64=4.74 for G=1 (and we could also add these to the table if desired). We could thus also estimate measures of multiplicative interaction. We could moreover estimate the risk ratios for G across strata of E: e.g. 8.64/1=8.64 for E=0 and 40.91/6.09=6.72 for E=1 (and we could present these in the table if desired). And we could moreover estimate measures of additive interaction from the information in Table 6: RERIRR=40.91−8.64−6.09+1=27.18>0. The presentation of interaction analyses in Table 6 thus gives the reader far more information (using a single common reference category) than the presentation in Table 5 (using multiple reference categories). Presenting interaction analyses using a common reference category such as the presentation in Table 6 is thus to be preferred. If the study is a cohort study then it may be even further preferable to present the actual risks, as in Table 1, in the cells of the table, rather than the risk ratios (Botto and Khoury, 2001; Knol and VanderWeele, 2012).

Knol and VanderWeele (2012) further suggested that when interaction and effect modification analyses are presented the following items all be given in a table: (1) risk differences or relative risks (or odds ratios if risk differences or relative risks cannot be calculated) for each (G,E) stratum with a single reference category (possibly taken as the stratum with the lowest risk of the outcome); (2) risk differences, relative risks, or odds ratios for G within strata of E, and for E within strata of G; (3) interaction measures on additive and multiplicative scales, along with confidence intervals and p-values for these; (4) the exposure-outcome confounders for which adjustment has been made either for one of the exposures (for effect modification/heterogeneity analyses) or for both of the exposures (for interaction analyses) with clear indication of whether attempt is being made to control for one or two sets of confounding factors. Knol and VanderWeele (2012) also considered different layout options for this information and how to further extend such presentations when one or both exposures has more than two levels. If multiple different interaction analyses are conducted in the same paper and presented in the same table, it may be desirable to put all of these items on a single line of a table so that multiple interactions analyses can be presented in the same table.

Careful thought should be given to presenting interaction analyses, so that the reader has the maximum amount of information available. In almost all cases, interaction analyses with a single reference group should be presented. Failure to do so will obscure information from the reader.

2.8 Qualitative interaction

In some cases, we might think that an exposure has a positive effect for one subgroup and a negative effect for a different subgroup. Such instances are sometimes referred as “qualitative interactions” or “crossover interactions” (Peto, 1982; Gail and Simon, 1985).^[7] Unlike statistical interactions in which the effects within two subgroups are both in the same direction, but simply differ in magnitude, qualitative interactions do not depend on the scale that is being used (de González and Cox, 2007). If there is a qualitative interaction on the difference scale, there will also be a qualitative interaction on the ratio scale.

As an example of such qualitative interaction, Gail and Simon (1985) considered data from a trial of two therapies for breast cancer, one of which does and the other of which does not involve tamoxifen. For young patients under age 50 with low progesterone receptor levels, the treatment without tamoxifen led to higher proportions who were disease-free after 3 years. However, for all other groups (who were either older, or had higher progesterone receptor levels, or both) the treatment with tamoxifen led to higher proportions who were disease-free after 3 years. Here, we would likely want to give young patients with low progesterone receptor levels the treatment without tamoxifen and others the treatment with tamoxifen.

In an example like this, we see then that qualitative interaction is very important in decision-making. We discussed above that in settings in which the intervention is beneficial for everyone but the magnitude of the benefit varies across subgroups, additive interaction can be useful in assessing whether it would be better to target the intervention to some subgroups rather than others if resources are limited. However, in such settings, if resources are not limited and the intervention is beneficial for everyone we may well want to treat all subgroups. Qualitative interaction, in contrast, has implications for treatment or interventions decisions even if resources are unlimited. In the presence of qualitative interaction, we do not want to treat all subgroups, because the treatment is in fact harmful in some subgroups. If qualitative interaction is present, it is thus important to be able to detect it.^[8]

Several statistical approaches have been developed for testing for such qualitative interaction (e.g. Gail and Simon, 1985; Piantadosi and Gail, 1993; Pan and Wolfe, 1997; Silvapulle, 2001; Li and Chan, 2006). The details of these various approaches and their power properties do vary, but they all essentially coincide when one is simply testing for qualitative interaction between two subgroups. The approaches differ when examining qualitative interaction across three or more subgroups.^[9] When testing for qualitative interaction across two subgroups one particularly simple approach (Pan and Wolfe, 1997) to test for a qualitative interaction at the 5% significance level is to construct 90% confidence intervals for the exposure effect in each of the two subgroups. If, on a difference scale say, one of the 90% confidence intervals lies entirely above 0 and the other lies entirely below 0, then one would reject the null hypothesis of no qualitative interaction. Note that only 90% confidence intervals (not 95%) need to be constructed here. These confidence intervals will be narrower than the usual 95% confidence intervals. One could alternatively carry out the analysis on a ratio scale and construct 90% confidence intervals for the effects in each of the subgroups and examine whether one of these 90% confidence intervals was completely above 1 and whether the other was completely below 1.

A special case or limit case of qualitative interaction is what is sometimes called a pure interaction in which the exposure has no effect whatsoever in one subgroup but does have an effect in a different subgroup. Like qualitative interactions, pure interactions do not depend on the scale being used. An example of such a “pure” interaction might include certain genetic variants on chromosome 15q25.1 which seem to only affect lung cancer for individuals who smoke and otherwise appear to have no effect for those who do not smoke (Li et al., 2010). We will consider this example further below.

2.9 Synergism and mechanistic interactions

Thus far, we have been considering different notions of statistical interaction and their interpretation. We noted above that such notions of interaction were scale dependent. In this section, we will consider drawing conclusions about more mechanistic forms of interaction. We might say that a “sufficient cause interaction” is present, if there are individuals for whom the outcome would occur if both exposures were present but would not occur if just one or the other exposure were present (VanderWeele and Robins, 2007, 2008). If we let Dge denote the counterfactual outcome (the outcome that would have occurred) for each subject if, possibly contrary to fact, G had been set to g and E had been set to e, then a sufficient cause interaction is present if for some individual D11=1 but D10=D01=0. This is in some sense a “mechanistic interaction” insofar as when both exposures are present the outcome is turned “on” but when only one or the other exposure is present the outcome is turned “off”. It can furthermore be shown that if such a sufficient cause interaction is present, then within Rothman’s sufficient cause framework (Rothman, 1976) there must be a sufficient cause for D which has both G and E as components (VanderWeele and Robins, 2007, 2008). This is thus sometimes called “synergism” between G and E in the sufficient cause framework. Note that a sufficient cause interaction does require some individual with D11=1 but D10=D01=0 but does not require D00=0 for this individual. Further below we will also consider an even stronger notion of “mechanistic interaction” which requires some individual for whom D11=1 and D10=D01=D00=0. However, we will begin our discussion of mechanistic interaction with the slightly weaker notion of a sufficient cause interaction, as this is all that is required for synergism between G and E within the sufficient cause framework.

Additive interaction is sometimes used to test for such mechanistic or sufficient cause interaction. However, having positive additive interaction only implies such sufficient cause interaction under additional assumptions. If it can be assumed that both exposures are never preventive for any individual (formally, if Dge is non-decreasing in g and e for all individuals), then provided control is also made for confounding of both exposures,^[10] positive additive interaction, p11−p10−p01+p00>0, suffices for sufficient cause interaction (Greenland et al., 2008; VanderWeele and Robins, 2007). The assumption that neither exposure can ever be preventive for any individual is sometimes referred to as a positive “monotonicity” assumption; it is a strong assumption. In some contexts, it might be plausible. For example, we would probably never think that smoking is protective for lung cancer for any individual. There may be some persons for whom smoking causes lung cancer, there may be others for whom smoking is neutral, but we would never think that smoking prevents lung cancer for anyone (i.e. that they would not have lung cancer if they smoked, but that they would have lung cancer if they did not smoke). Thus the positive monotonicity assumption for the effect of smoking on lung cancer may be plausible. But in other cases the assumption may be less plausible. For example, if we were to consider the effect of alcohol consumption on stroke, alcohol may be protective for stroke in some persons but causative for others; the monotonicity assumption would not be plausible here. Positive monotonicity requires that the effect is never preventive for the outcome for any person in the population. Importantly, to assess sufficient cause interaction simply by examining whether additive interaction is positive requires that the effects of both exposures on the outcome be monotonic. This will in many contexts be a strong assumption, and it is an assumption that is not possible for verify empirically; it must be established on substantive grounds.

Fortunately, it is also possible to test for sufficient cause interaction even without such monotonicity assumptions but the standard tests for positive additive interaction no longer suffice. Alternative tests must be used. VanderWeele and Robins (2007, 2008) showed that if the effect of the two exposures were unconfounded then

would imply the presence of a sufficient cause interaction. This is a stronger condition than regular positive additive interaction which only requires p11−p10−p01+p00>0, because, with the condition p11−p10−p01>0, we are no longer adding back in the outcome probability p00 for the doubly unexposed group. This condition for a sufficient cause interaction, without making monotonicity assumptions, thus does not correspond to, and is stronger than, the regular test for additive interaction, or than simply examining whether interaction is positive in a statistical model (VanderWeele, 2009b). In these various cases, the magnitude of the contrast p11−p10−p01+p00 with monotonicity or p11−p10−p01 without monotonicity in fact gives a lower bound on the prevalence of individuals manifesting sufficient cause interaction patterns (VanderWeele et al., 2010).

If data are only available on the ratio scale, then if both exposures have positive monotonic effects on the outcomes, we can test for sufficient cause interaction by the condition RERIRR>0. Likewise, the condition p11−p10−p01>0 without imposing monotonicity assumptions can be expressed in terms of RERIRR as RERIRR>1; again this is stronger than simply the ordinary condition for additive interaction RERIRR>0. However, RERIRR still can be used in a straightforward way to test for such sufficient cause interaction by testing whether RERIRR>1 rather than simply RERIRR>0.

Note that when the empirical conditions above are satisfied, the conclusion is that there are some individuals for whom D11=1 and D10=D01=0; the conclusion is not that all individuals have this response pattern. Note also that these conditions given here are sufficient but not necessary for sufficient cause interaction, i.e. if these conditions are satisfied then a sufficient cause interaction must be present, but if the conditions are not satisfied, then there may or may not be a sufficient cause interaction – one simply cannot determine this from the data. The conditions given here are the weakest possible empirical conditions to test for sufficient cause interaction without making further assumptions (VanderWeele and Richardson, 2012).

VanderWeele (2010a, 2010b) discussed empirical tests for an even stronger notion of interaction. We might say that there is a “singular” or “epistatic” interaction if there are individuals in the population who will have the outcome if and only if both exposures are present; in counterfactual notation, that is, there are individuals for whom D11=1 but D10=D01=D00=0. In the genetics literature, when gene–gene interactions are considered, such response patterns are sometimes called instances of “compositional epistasis” (Phillips, 2008; Cordell, 2009) and constitute settings in which the effect of one genetic factor is masked unless the other is present. VanderWeele (2010a, 2010b) noted that if the effects of the two exposures on the outcome were unconfounded then

would imply the presence of such an “epistatic interaction”. Again this is an even stronger notion of interaction; in this condition for “epistatic interaction” we are now subtracting p00. The condition p11−p10−p01−p00>0 expressed in terms of RERIRR is equivalent to RERIRR>2.

For epistatic interactions, if the effect of at least one of the exposures is positive monotonic (Yge is non-decreasing in at least one of g or e), then p11−p10−p01>0 suffices for an epistatic interaction and tests for RERIRR>1 could be used; if the effects of both exposures are positive and monotonic, then p11−p10−p01+p00>0 suffices and tests for RERIRR>0 could be used to test for an epistatic interaction (VanderWeele, 2010a, 2010b). These conditions are likewise sufficient but not necessary for an epistatic interaction; if these conditions are satisfied, then an epistatic interaction must be present, but if the conditions are not satisfied, then an epistatic interaction may or may not be present. Note also that when the empirical conditions above are satisfied, the conclusion is that there are some individuals for whom D11=1 but D10=D01=D00=0; the conclusion is not that all individuals have this response pattern. The various results are summarized in Table 7.

The sufficient conditions given here for mechanistic interaction require that control has been made for confounding of the effects of both exposures. The sufficient conditions for RERIRR for mechanistic interaction in Table 7 still apply when adjustment is made for confounders, e.g. when the relative excess risk due to interaction is calculated using logistic regression as described above adjusting for covariates.^[11]

In assessing additive interaction using RERIRR, it thus is useful to examine not only whether the estimate and confidence interval for RERIRR are greater than 0 (i.e. whether there is additive interaction) but also whether the estimate and confidence interval for RERIRR are all greater than 1 or are all greater than 2. This is because RERIRR of this magnitude would provide evidence for mechanistic interaction (sufficient cause or epistatic interaction) without the need for additional assumptions. The RERIRR scale is in some sense the natural scale on which to assess mechanistic interaction and has the thresholds of 0, 1, and 2 for varying degrees of evidence (according to the strength of the assumptions needed for the conclusion). We noted above that RERIRR cannot be used to assess the magnitude of the underlying additive interaction for risks, but we see here that although its magnitude does not necessarily correspond to the magnitude of the additive interaction for risks, the magnitude of RERIRR does give differing degrees of evidence for mechanistic interaction.^[12]

As an example, Bhavnani et al. (2012), using age-standardized measures, reported that risk ratios for diarrheal disease across groups infected with rotavirus and/or Giardia. With the doubly unexposed group as the reference category, the risk ratio for rotavirus (in the absence of Giardia) is 2.63, the risk ratio for Giardia (in the absence of rotavirus) is 1.13, and the risk ratio when both rotavirus and Giardia are present is 10.72. This gives RERIRR=10.72−2.63−1.13+1=7.96 (95% CI: 3.13, 18.92). The value of RERIRR and its entire 95% confidence interval exceed the value 2, suggesting strong evidence for mechanistic interaction (both “sufficient cause” and “epistatic” interaction) even in the absence of any monotonicity assumptions.

Although it is beyond the scope of the current paper extensions of these ideas are available for exposures with more than two levels (VanderWeele, 2010a, 2010b, 2010d) and for multi-way interactions between three or more exposures (VanderWeele and Robins, 2008; VanderWeele and Richardson, 2012) as well as for settings with causal antagonism in which the presence of one exposure may block the operation of the other (VanderWeele and Knol, 2011b) See VanderWeele (2014b) for an overview. In the next section, we will discuss how even these so-called mechanistic interactions (sufficient cause or epistatic interactions) considered here give limited information about the underlying biology.

3.1 Limits of inference concerning biology

Although tests for sufficient cause interaction, like those considered in the previous section, can shed light on whether there are individuals for whom the outcome would occur if both exposures are present but not if just one or the other is present, it should be noted, that even such “mechanistic interaction”, does not imply that the two exposures are physically interacting in any real sense (Siemiatycki and Thomas, 1981; Thompson, 1991; VanderWeele and Robins, 2007; Phillips, 2008; Cordell, 2009). To see this, suppose that G1 and G2 are two genetic factors. Suppose that when G1=1 protein 1 is not produced and that when G2=1 protein 2 is not produced. Suppose that the outcome D occurs if and only if neither protein 1 nor protein 2 is present. We then have an epistatic interaction because the outcome occurs if and only if G1=1 and G2=1, but we do not have physical interaction here. It is precisely the absence of the proteins that gives rise to the outcome; there simply is nothing to physically interact here.

We should thus distinguish between (i) statistical interaction on the one hand and (ii) mechanistic interaction (e.g. the outcome occurs if both exposures are present but not if just one or the other is present) on the other, and finally, (iii) “biological” or “functional” interaction in which the two exposures physically interact to bring about the outcome (Phillips, 2008; Cordell, 2009; VanderWeele, 2010a, 2011a). In the example just given, we have mechanistic interaction but not “functional” or physical interaction. Thus, although we can sometimes empirically draw conclusions about mechanistic interaction from data, empirical tests will not in general allow us to draw conclusions about functional or physical interaction between exposures and it is important to understand the limits of the conclusions being drawn about these alternative forms of interaction.

Other examples of the limitation of biologic inference concerning interaction were given by Siemiatycki and Thomas (1981). Consider, for example, a setting in which for the outcome to occur two stages of disease development must take place. Several theories for the development of cancer follow this model. Suppose that the two exposures of interest, G1 and G2 say, affect different stages: G1 acts on stage 1 and G2 acts on stage 2. Suppose also in this example that stage 1 and stage 2 are completely independent of each other. Assume that the baseline probability of stage 1 occurring is 1% and the baseline rate of stage 2 occurring is also 1%, so that the baseline likelihood of disease is 0.01%. Suppose that G1 increases the probability of stage 1 occurring from 1% to 2% and G2 increases the probability of stage 2 occurring from 1% to 5%. Suppose, however, that the presence of G2 in no way alters the effect of G1’s increasing the probability of stage 1 occurring from 1% to 2%; i.e. the probability of stage 2 is 1% if G1=0 and 2% if G1=2, irrespective of whether G2 is present or absent. Suppose, similarly, that the presence of G1 in no way alters the effect of G2’s increasing the probability of stage 2 occurring from 1% to 5%. Here then we seem to have no interaction between G1 and G2 at the biologic level.

As noted above, if neither exposure is present (G1=0 and G2=0), then the risk of stage 1 and stage 2 are both 1% and the overall likelihood of the outcome is 1%×1%=0.01%. If just G1 is present (G1=1 and G2=0), then the risk of stage 1 is 2% and the risk of stage 2 is 1% and the overall likelihood of the outcome is 2%×1%=0.02%. If G1=0 and G2=1, then the risk of stage 1 is 1% and the risk of stage 2 is 5% and the overall likelihood of the outcome is 1%×5%=0.05%. If G1=1 and G2=1, then the risk of stage 1 is 2% and the risk of stage 2 is 5% and the overall likelihood of the outcome is 2%×5%=0.10%. In this example, our measure of multiplicative interaction is p11p00p10p01=0.10%(0.01%)0.02%(0.05%)=1. However, our measure of additive interaction is

We have positive additive interaction but no biologic interaction in this example. Here our conditions for sufficient cause interaction are satisfied, since

,and even our conditions for “epistatic” or “singular” interaction,

are also satisfied. But again we saw that there was no interaction between G1 and G2 at the biologic level. How are we to make sense of this? What we can conclude from the condition for a epistatic or singular interaction, say, are that there are some individuals who would have the outcome if both exposures were present but who would not if just one or the other or neither exposure were present. But we see here that not even this necessarily indicates interaction at some fundamental biologic level. We have this form of “singular” or “sufficient cause” interaction because, if both exposures are present, 0.10% have the outcome and this cannot be accounted by those individuals whose outcome only required the first exposure (0.02%) or only the second (0.05%) or who required neither (0.01%). Even if these three groups were mutually exclusive, they would not account for the risk of 0.10% that occurs if both exposures are present (0.10%−(0.02%+0.05%+0.01%)=0.02%>0). There must be some individuals for whom the outcome occurs if and only if both exposures are present. But again, this does not, as this example shows, indicate biologic interaction in any fundamental biologic sense.^[13]

We can assess statistical interaction (on any scale we choose), we can assess additive interaction to determine how best to allocate interventions, and we can assess “sufficient cause” or “epistatic/singular” interaction to determine whether there are individuals who would have the outcome if both exposures were present but not if only one or the other were present. All of these may provide some insight into the underlying biology, but we have no way of going from any of these forms of interaction which we can assess with data directly to the underlying biology itself.

In some earlier literature, sufficient cause synergism was sometimes earlier referred to as “biologic interaction” (e.g. Rothman and Greenland, 1998); sometimes even just additive interaction was even referred to as “biologic interaction” (e.g. Andersson et al., 2005). However, as we have seen in the examples above, neither statistical additive interaction nor even sufficient cause interaction or epistatic interaction necessarily tells us anything about physical or functional interactions. Statistical analyses can only tell us limited information about the underlying biology (Siemiatycki and Thomas, 1981; Thompson, 1991; Rothman and Greenland, 1998; Cordell, 2002). Because of this there has been a suggestion to move away from the use “biologic interaction” for sufficient cause interaction or synergism in the sufficient cause framework (cf. Lawlor, 2011; VanderWeele, 2011a). It may be more appropriate to refer to these sufficient cause or epistatic interactions as “mechanistic interactions”; these are still cases in which both exposures together turn the outcome “on” and the removal of one turns the outcome “off” and thus the “mechanistic” description seems potentially appropriate. If even this is thought to be language that is too strong (if “mechanistic” is still thought to indicate biology rather than indicating “on” and “off”), then simply using the terms “sufficient cause interaction” or “singular interaction” may be best.

3.2 Attributing effects to interactions

3.3 Case-only designs

Another more recent approach concerning statistical interaction is also worth noting. Consider the statistical interaction β3 in the log-linear model:

Suppose now also that the distribution of the two exposures, G and E, are independent in the population. This assumption may be plausible in many gene–environment interaction studies. Suppose further that data are only collected on the cases (D=1). It can be shown that under this independence assumption, the odds ratio relating G and E among the cases is equal to the interaction measure on the multiplicative scale β3 (Yang et al., 1999; cf. Piergorsch et al., 1994):

Somewhat surprisingly, to get measures of multiplicative interaction, all that is needed is data on G and E among the cases. The use of the odds ratio relating G and E among the cases is referred to as the “case-only” estimator of interaction. With the case-only estimator we can estimate the interaction parameter β3, but we cannot estimate the main effects of the log-linear regression, β1 and β2.

The case-only estimator depends critically on the assumption that the distribution of the two exposure are independent in the population and can be quite biased if this assumption is violated (Albert et al., 2001). However, under this assumption of independence in distribution, the case-only estimator is in fact more efficient than using the standard estimate from a log-linear regression (Yang et al., 1997).

The same result holds for statistical interaction in logistic regression

under the assumption that the outcome is rare (Piergorsch et al., 1994). The result for log-linear models does not require a rare outcome. Sometimes, for logistic regression, the independence assumption is articulated as one of independence of G and E among the non-cases. For a rare outcome, this is approximately equivalent to independence in the population.

The result also holds for log-linear or logistic regression if we control for covariates. The conditional independence assumption is then that the distributions of G and E are independent conditional on C. Estimates and confidence intervals for the case-only estimator can be obtained by running a logistic regression of G on E and C among the cases:

The coefficient and confidence interval for θ1 in this regression on the cases will equal that of the product term coefficient in the log-linear model with covariates provided the distributions of G and E are independent in the population and will equal the product term coefficient in the logistic model with covariates, in addition, that the outcome is rare.

Note that in all of these cases, to interpret the multiplicative interaction parameter estimate from the statistical model as causal interaction on a multiplicative scale, it would be necessary to assume that the effects of both exposures on the outcome are unconfounded (conditional on covariates C). To interpret the parameter estimate as a measure of effect heterogeneity on the multiplicative scale, it would be necessary to assume that the effect of one of the exposures on the outcome is unconfounded (conditional on covariates C). In a case-only study, simply assuming that the effect of one exposure on the other exposure is unconfounded does not suffice to give a causal interpretation for the effects of either or both exposures on the outcome Y.

As an example, Bennet et al. (1999) used data on non-smoking lung cancer cases and reported exposure status for GSTM1 genotype and passive smoking as in Table 8.

Using data only on the cases we have that the estimate of multiplicative interaction is