Casual Diagrams

The purpose of this page is to document information on types of casual diagrams and how they are used. This includes background on the set of of different diagrams, cause vs correlation, mediation, and effect modification.

Directed Acyclic Graphs (Causal Diagrams)

Important

The figures represented in this section represent directed acyclic graphs/causal diagrams. These figures are distinct from compartamental model diagrams (such as SIR models). DAGs for causal diagrams are commonly represented as circles connected by arrows, and compartmental model diagrams are commonly represented as squares connected by arrows; we will follow this convention here.

Additionally, for the purposes of directed acyclic graphs, variables will be labeled with capital letters (A, B, C, etc.) and arrows will be labeled with lower case letters (a, b, c, etc.).

Introduction to Directed Acyclic Graphs

Directed acyclic graphs (DAGs) are composed of variables (nodes of the graph) that are linked together by directional arrows (arcs of the graph), in such a way that the arrows do not form any directed cycles. For our purposes here, DAGS will represent causal diagrams. Critically, the solid arrows in DAGs represent a causal relationship between an exposure variable (start of the arrow) and outcome variable (end of the arrow), representing the directional aspect of DAGs. Notably, a directional arrow in a DAG does not offer any information about whether the exposure causes an increased or decreased probability of the outcome, only that there is some causal relationship between the exposure and outcome.

The acyclic nature of DAGs is that there cannot be feedback loops between any variables in the graph. In this way, the arrows in DAGs can be interpreted as the passage of time so that the exposure (cause) must always occur temporally before the outcome (effect). See the diagram below for an example of an inappropriate and appropriate DAG with regard to temporality.

Note

The figure below represents a feedback loop between two variables; however feedback loops that involve more than two variables are also not appropriate for use in causal diagram DAGs.

Applications, Assumptions, and Limitations of Directed Acyclic Graphs

DAGs are used in epidemiology to represent a network of relationships between several variables, which in turn helps to guide the selection of variables that will need to be measured or considered in a given study/project. Further, the exact relationship between variables in a DAG will dictate how to treat or consider a specific variable in that study/project by helping to indentify potential confounding, intermediate, or mediating variables between a given exposure and outcome of interest (see the Causal Relationships section for definitions).

However, DAGs are limited in that they require prior causal knowledge about the variables that may be causally related to a given exposure and outcome of interest. Therefore, there may be uncertain, unmeasured, or unknown variables that cannot be represented in a given DAG. Further, DAGs do not allow for easy representation of whether a relationship is positive or negative, the magnitude of a causal relationship, or effect modification. Note that alternative formats may be utilized to represent these factors as needed, such as varying arrow weights, denoting \(+\) and \(-\) signs with arrows, etc.; however, these formats are not shown in this section.

For the purposes of this section of our documentation, we will assume that each DAG is completely accurate, represents all relevant variables in a given causal network and that there are no unrepresented variables.

Types of Pathways Within Directed Acyclic Graphs

A path in a DAG is defined as any route drawn through arrows that link two variables regardless of the direction of the arrows.

Directed Paths

Directed paths are those in which variables are connected through arrows that all flow in the same direction. See below for an example of a directed path between variables A and D.

In the case of a directed path between two variables, those variables will be causally related.

Undirected Paths

Undirected paths are those in which variables are connected through arrows that do not all flow in the same direction. The two cases of undirected paths covered here include backdoor paths and colliders.

In the case that there is an undirected path (and no directed path) bewteen two variables, those variables will NOT be causally related, although they may be associated in some way.

Backdoor Paths

Backdoor paths are those in which two variables are connected via a common cause. The simplest example of this is when two variables that are linked via a variable that has two arrows flowing away from it. See below for an example in which variables Y and Z are connected via a backdoor path through variable X.

Notably, if there were more variables between variables X and Y or variables X and Z, there would still be a backdoor path between variables Y and Z.

In the case of a backdoor path between two variables (and no directed path), there will be an association (due to a common cause between them), but no causal relationship between the two variables.

Colliders

Colliders are variables that have more than one cause; in other words, where pathways collide and a variable has two arrows flowing toward it. See below for an example in which variable Z is a collider on the path between variables X and Y.

In the case that two variables are linked through a path with a collider (and there is no directed or backdoor path between them), there will be no association or causal relationship between the two variables. Paths bewteen two variables with a collider are referred to as a “closed paths,” while paths without colliders are referred to as “open paths.”

Summary

DAG Pathways

Path Name/Term	Description	Direction	Open or closed	Association
Directed path	Path with arrows flowing in same direction	Directed	Open	Causal relationship
Open backdoor path	Path with arrows flowing in different directions without a collider	Undirected	Open	Non-causal association
Closed path	Path with a collider	Undirected	Closed	No association

Identifying Confounding Using Directed Acyclic Graphs

As discussed previously in this documentation, confounding arises when a given exposure and outcome share a common cause (Confounding). This section will help to identify potential confounding variables in a given causal network that may be less explicit than the example(s) presented in the Confounding section.

For the remainder of this section, we will focus on the relationship between a particular exposure (E), shown in blue, and a particular outcome (O), shown in purple.

In the context of DAGs, confounding may occur when there is an open backdoor pathway (unblocked backdoor pathway with no colliders) between an exposure and outcome of interest. Therefore, any variable that can be used to block an open backdoor path between a given exposure and outcome is a confounder with regard to the relationship between that exposure and outcome.

“Blocking” an open backdoor path can be done via randomization of that variable between exposure groups in the context of a randomized controlled trial or via conditioning (adjustment via stratification or other methods) in the context of an observational study on that variable. In the following diagrams, variables that are blocked in this way will be represented as squares rather than circles; when this is the case, assume that a pathway with a square variable is a closed pathway. Notably, it is not necessary to condition on all variables on a backdoor path; the path can be closed by conditioning on a minimal set of variables and there may be more than one possible minimal set of variables. See below for possible options for closing backdoor paths by conditioning a minimal set of variables (in this case a single variable).

Finally, do not be fooled by the following situations for which there is no need to condition! The following examples represent DAGs for which there is no open backdoor path (backdoor paths are closed via colliders), or in other words, there is no causal pathway that affects both the exposure and the outcome. Therefore, there is no confouding with regard to the relationship between the exposure and the outcome and no need to condition on any confounding variable.

In fact, if we were to condition on a collider (i.e. variable Y in example 1 or variable X in example 2), we would introduce dependence between the colliding variable’s parent variables (i.e. variables X and Z in example 1 and variables E and Y in example 2). In other words, conditioning on a collider between two variables opens the previously closed path between those variables and introduces bias in the evaluation of the causal relationship between them. Therefore, one should not condition on colliding variables between an exposure and outcome.

Denoting Non-Causal Associations

So far in this section, we have only made use of solid arrows to represent explicit causal relationships. However, situations may arise in which there is an observed association between two variables for which the driving force behind that association may be unknown, although it is not believed to be (or there is insufficient evidence to conclude) a direct causal relationship between the two variables.

In this case, it may still be useful to represent this association in a DAG without drawing a direct causal relationship between these two variables. There are two potential ways to do so.

The first approach is to introduce an additional variable into the dag, termed “U”, or “Unknown” that is causally related to the two associated variables, as shown below. Here, it can be seen that because variables A and B share a common cause (U), they will be associated, although they are not causally related. This approach allows us to use the DAG to identify confounding in the relationship between the exposure and outcome in the way described in this section above (identifying any open backdoor paths, which may flow through the variable U).

The second approach is to represent the association between the two variables with a dashed line. For our purposes, dashed lines in DAGs will represent a non-causal association between two variables as shown in the figure below. While this format does not allow us to easily identify open backdoor paths in the way described in this section, it still allows us to identify confounding using the definition provided in the Confounding section. Additionally, this method allows us to represent non-casual associations that we may want to model explicitly, such as a correlation coefficient between two variables.

For our purposes, the two approaches shown in this section for representing non-causal associations between two variables (a common cause of an unknown variable and a dashed connecting line) are equivalent representations.

Note

Dashed lines will represent non-causal associations as described above in all causal diagram DAGs in the Vivarium Research repository.

Causal Relationships

In this context, causal relationships imply that there is a direct cause and effect relationship between two traits (generally an exposure and an outcome). Notably, we hope to differentiate causal relationships (which have a direct cause and effect relationship) from correlated relationships (which have a relationship, but it may be driven by something other than a direct cause and effect). As it turns out, distinguishing between correlation and causation can be quite a challenging task and many fields, including epidemiology, are devoted to the process of causal inference, or drawing a conclusion about a causal relationship based on the available evidence.

A term that is often used in causal inference is the counterfactual. The counterfactual refers to an alternate reality in which only a single variable has changed and all else has remained exactly the same.

For instance, suppose you’ve finished work and you’re trying to determine how to get down to the international district for dinner. You go to your maps application and ask What is the quickest route to my destination? It tells you that based on the current time, weather, day of the week, road work conditions, etc. that you should take the light rail.

So you leave the office, walk a few blocks to the westlake station, and catch the train. Two stops in, your train gets stopped behind a broken down bus. You decide to get off the train and walk the remaining distance. Arriving ten minutes late to dinner, you think to yourself Would I have arrived on time if I took the bus instead?

As illustrated here, by definition the counterfactual question is impossible to directly answer because it is a purely hypothetical question without direct supporting evidence; we can only use what we know to make a guess at what might have happened in the counterfactual scenario. Consider the following example:

Say that we wanted to evaluate the causal realtionship between smoking and lung cancer. Hypothetically, we could compare lung cancer rates between 1954 when smoking was at its peak in the US and 2020 when smoking rates in the US are lower. However, you can quickly imagine additional differences between 1954 and 2020 US that may also impact the rates of lung cancer, such as differences in air pollution due to automobiles and the rise of electronic cigarettes.

Therefore, while the comparison between 1954 and 2020 US may be interesting and useful, it is not a true counterfactual comparison. Instead, a counterfactual scenario could be conceptualized as “what would the lung cancer rate in the US be in 1954 if no one smoked and all else was equal?” Then, we could evaluate the independent effect of smoking on lung cancer without interference from any other factors.

However, we cannot wave a magic wand and explore the lung cancer rate in this alternative universe in 1954 to answer this question. Luckily, there are several methods in the field of epidemiology that attempt to answer conterfactual questions regarding causal relationships through randomized controlled trials and other types of studies.

One way in which causal inference is performed for a particular relationship between an exposure and outcome is assessment based on the Bradford Hill criteria for causation. The Bradford Hill criteria are a group of principles that may be used in evaluating the epidemiologic evidence of a causal relationship such that the more criteria that are satisfied, the more likely it is that a causal relationship exists. The criteria are listed below:

• Strength/Effect Size: The larger the association, the more likely that it is causal.

• Consistency/Reproducibility: Consistent findings observed by different people in different places increase the likelihood of causality.

• Specificity: The more specific the association between a cause and an effect, the more likely that it is causal.

• Temporality: The effect must occur after the cause.

• Biological Gradient/Dose-Response Relationship: Greater exposure should generally lead to greater observed effect.

• Plausibility: A plausible mechanism between cause and effect is helpful (although limited by current knowledge).

• Coherence: Coherence between epidemiological and laboratory findings increases the likelihood of a causality.

• Experiment: Experimental evidence between the cause and effect generally supports a causal relationship.

• Analogy: Analogies or similarities between the observed associations and other associations exist generally support a causal relationship.

• Reversibility: If the cause is deleted, the effect should also disappear.

A particularly relevant criterion listed above is temporality, which declares that in order for a relationship to be causal, the cause or exposure must occur before the effect or outcome chronologically. When this criterion is not satisfied, there is a risk for reverse causalility, in which the causal relationship occurs in the opposite direction as expected.

While these criteria are a useful guide for assessing whether there is sufficient evidence to conclude that a relationship is causal, there are several concepts that should be considered when thinking about causality between an exposure and an outcome. Relationships that complicate our understanding of causality, including confounding, intermediates, effect modification, and mediation are discussed in the following subsections.

Notably, in the following sections, solid arrows are used to depict causal relationships directionally between a cause/exposure and effect/outcome.

Confounding

What is confounding?

Confounding occurs when an estimate of the association between an exposure and a health outcome is mixed together with the effect of another exposure on the same health outcome, and the two exposures are associated. The presence of a confounding exposure biases the estimate of the effect of the exposure of interest on the health outcome.

The bias can be negative (resulting in underestimation of the exposure effect), or positive (overestimation of the exposure effect), or can even reverse the apparent direction of effect. Confounding should always be addressed when assessing causality and failure to account for confounding leads to incorrectly concluding that an effect or its magnitude is due to one, rather than another variable.

In order for a factor to be a confounder (C), it must meet the following criteria:

1. Must be a risk factor, or a surrogate measure of the risk factor, for the outcome (O) of interest in those who are unexposed to the exposure (E) being investigated.

2. Must be correlated, positively or negatively, with the exposure (E). If the study population is stratified into exposed and unexposed groups, this means that (C) has a differential distribution in the two groups.

3. In addition, (C) should not be an intermediate step on the causal pathway between the exposure (E) and outcome (O) being investigated. If this is the case, (C) may in fact be an intermediate or a mediator . In other words, the exposure (E) should not cause the confounder (C).

Note

Criteria 2 says that the confounder needs to be correlated to the exposure. This means they can either be simply correlated, or they can have a causal relationship. If causal, the direction of the causal relationship has to be from the confounder (C) to the exposure (E) and not the other way round as noted in criteria 3.

Todo

we should also note how we will apply our knowledge of confounding in our models. like, when do we need to be careful of confounders? like only when we interpret our effect sizes from the literature? What about GBDs assumptions of confounding? Do all gbd models (the RRs for the risk cause-models) have assumptions of causal, with no confounding?

An example: Imagine that you are interested in knowing whether smoking (our risk factor of interest) influences the risk of coronary heart disease (CHD) in men aged 18 to 64 years. You conduct a cohort study with an exposed group of male smokers in this age group from the general population, and compare their risk of CHD after a number of years to that of an unexposed group of non-smoking males in the same age group. You would expect to find a higher incidence of CHD among smokers. However, males who smoke are also likely to have a higher alcohol intake, which also increases the risk of CHD. Thus, the effect that you observe for the smoking-CHD association is mixed-up/confounded by/confused with with the effect of the association between alcohol intake and CHD. Without taking account of differences in alcohol intake between smokers and non-smokers, the magnitude of the smoking-CHD association estimated from the study may be higher than the true value, leading to incorrect conclusions.

The criteria for alcohol to be a confounding factor for the smoking-CHD relationship is met because:

1. Alcohol intake is a risk factor for CHD in non-smokers. In other words the relationship between alcohol and CHD is not dependent on smoking status.

2. Smokers generally have a higher alcohol intake (in most populations).

3. Finally, alcohol intake is not on the causal pathway between smoking and CHD (smoking does not in itself cause people to drink more alcohol).

Note that the dotted line between smoking and alcohol indicates that we do not expect a ‘causal’ link between the smoking and alcohol. Rather, it indicates that the two are associated in the population.

How to identify confounding?

We look for confounding by stratifying (splitting) the data according to the proposed confounding factor and then examining the measures of effect of the exposure on the outcome in the different strata separately. If the stratum-specific measures of effect are similar to each other, but different from the crude measure of effect, this is evidence for confounding. We can now consider a numerical example to demonstrate how you can look for confounding in data from an epidemiological study.

An example: A report was published that made the novel claim that coffee consumption is associated with risk of cancer of the pancreas. Here, the exposure (E) is coffee consumption and the outcome (O) is cancer of the pancreas. The importance of this finding was disputed because it was pointed out that coffee consumption is associated with cigarette smoking, and smoking is known to be a risk factor for cancer of the pancreas. Thus, smoking may be confounding (C) the association between coffee consumption and risk of cancer of the pancreas.

(Smoking is a credible alternative explanation for the reported association between coffee and pancreatic cancer. While there are many other things that are associated with coffee drinking, for any of these things to provide a credible alternative explanation for the coffee-cancer relationship, they would have to be associated with cancer risk indepedent of coffee drinking [criteria 1].)

Suppose that the association between coffee consumption and pancreatic cancer was detected in a case-control study, where the basic data was as follows:

	Drinks coffee	Does not drink coffee
Cases	450	300
Control	200	250

From this data, it seems that the odds of coffee consumption among cases (450/300 = 1.5) is higher than that among controls (200/250 = 0.8), giving an odds ratio of 1.9.

Suppose we now look at the association between coffee consumption and pancreatic cancer separately for smokers and non-smokers. This is known as stratification.

The table below shows the data on coffee consumption and disease status for smokers and non-smokers (or stratified by smoking status):

	Smokers		Non-smokers
	Drinks coffee	Does not drink coffee	Drinks coffee	Does not drink coffee
Cases	400	200	50	100
Control	100	50	100	200
Odds ratio	(400/200)÷(100/50) = 1.0		(50/100)÷(100/200) = 1.0

If smoking had no influence on the association between coffee consumption and pancreatic cancer, then we would expect that the odds ratio would still be about 1.9, both in smokers and non-smokers. In fact, in our example, the odds ratio for both smokers and non-smokers is 1.0. In other words, after stratifying by smoking status, there appears to be no evidence of an association between coffee consumption and pancreatic cancer. The results support the suggestion that smoking confounded the association between coffee and risk of cancer of the pancreas. The statistical association between coffee drinking and cancer is still valid, but the explanation for this association is that it is largely due to unequal distribution of smoking behaviour among people who do, and do not, drink coffee.

Why should this be? We mentioned earlier that, in order for a factor to be a confounder, it must be associated with the risk factor under investigation. In our example, we can investigate whether this is true by examining the data from controls, since the distribution of all exposures in the control group should reflect the distribution of exposures in the population from which the cases originated.

The table below shows the association between the exposure (E), coffee consumption, and the confounder (C), smoking, among the controls [criteria 2]:

	Drinks coffee	Does not drink coffee
Smokers	100 (50%)	50 (20%)
Non-smokers	100 (50%)	200 (80%)
Total	200 (100%)	250 (100%)

We can see that, among coffee drinkers, 1 in 2 (50%) are smokers, whereas among those who do not drink coffee, only 1 in 5 (20%) are smokers. This observation satisfies the first criterion for a confounding factor, that it must be associated with the risk factor under investigation. The coffee drinkers and non-coffee drinkers are not comparable (similar) in their drinking habits. (* Note: In a cohort study, we could look at this association by constructing a similar table, but replacing the number of controls in each cell with the number of person-years at risk (or the number of persons at the start of follow-up if we are conducting an analysis of risks rather than rates)).

We also mentioned above that, for a factor to be a confounder, it should be a risk factor for the outcome and that this relationship is not dependent on exposure status [criteria 1]. In our example, we can confirm this by looking at the association between smoking and pancreatic cancer separately for those who drink coffee and those who do not:

	Drinks coffee		Does not drink coffee
	Smoker	Non-smoker	Smokers	Non-smokers
Cases	400	50	200	100
Control	100	100	50	200
Odds ratio	(400/50)÷(100/100) = 8.0		(200/100)÷(50/200) = 8.0

The odds of pancreatic cancer are 8 times higher among individuals who smoke than among individuals who do not smoke regardless of whether or not they drink coffee. This then satisfies the first criterion that the factor must be a risk factor for the disease in those unexposed.

Finally, we can be confident that smoking is not on the causal pathway between coffee drinking and pancreatic cancer, so the third criterion for being a confounder is satisfied.

It should now be clearer why smoking acts as a confounder in the association between coffee consumption and pancreatic cancer. Smoking is itself a risk factor for pancreatic cancer, and smoking is also differentially distributed between those who drink and not drink coffee. Thus, when we first looked at the overall association between coffee consumption and pancreatic cancer, the effect of coffee consumption was mixed up with the effect of smoking (because there are proportionately more smokers among those who drink coffee than among those who do not). But once we accounted for smoking by looking at the data separately for smokers and non-smokers, it became clear that there is, in fact, no evidence for an association between coffee and pancreatic cancer.

Having established that smoking appears to confound the association between coffee consumption and pancreatic cancer, the final step is to combine, or pool, the data across strata of smoking to obtain a combined, or pooled, estimate of the effect of coffee consumption on pancreatic cancer adjusted for the confounding effect of smoking. This pooled estimate is an average of the effect across all strata of smoking weighted by the size of each stratum. There are statistical methods for obtaining such pooled estimates (e.g. Mantel-Haenszel, regression). There are a number of strategies to minimise or deal with confounding, both when designing a study and in the analysis phase.

Note

as you can see, there is no real effect of coffee on cancer - coffee does NOT cause cancer! PHEWWW- we can caffeine away! This example showed that the purported relationship between coffee and cancer was in fact spurious. It was all because of smoking, smoking was the real culprit (isnt it always?)! It got ‘mixed-up’ with coffee cuz more coffee drinkers smoke so it made it seem like drinking coffee is a risk factor for smoking.

In vivarium, we should not have the need to be involved with proving causality. But we do need to make an assessment of whether the reported effect sizes we use from the literature are true estimates or they could be biased due to residual confounding that has not been fully addessed.

Todo

What we should look for re: confounding when assessing effect sizes

Intermediates

An intermediate variable as discussed in this section is defined as a variable between an exposure and outcome in a sequential causal chain, as demonstrated in the diagram below:

An Example of an Uncomplicated Intermediate

A (simplified) example that can demonstrate such a causal pathway is the relationship between the exposure of cigarette smoking, which causes the intermediate variable of accumulated tar in lungs, which in turn causes lung cancer (note: for the purposes of this example, assume that there is no direct causal relationship between cigarette smoking and lung cancer other than through the intermediate variable of accumulated tar in lungs).

Now, let’s say that we plan to enact an advertising campaign to reduce smoking in hopes of reducing population lung cancer rates. Our expected causal pathway would look like this:

Therefore, as we increase intervention coverage (assuming the intervention is effective), we would expect a decrease in population lung cancer rates, as these two variables are located on the same causal pathway.

An Example of a Complicated Intermediate

Now, let’s imagine that a brand new hypothetical medication was just created that dissolves tar in lungs that accumulates due to smoking and is now widely used in some areas. Our causal diagram would now look like this:

Quickly, we can now see that the relationship we previously knew between smoking and lung cancer is now impacted by the use of this hypothetical medication that affects the intermediate variable between smoking and lung cancer. Therefore, we can only expect lung cancer rates to decrease by the expected amount as a result of our marketing intervention in areas that do not widely use this medication.

Notably, intermediate variables may be relevant in situations in which the variable located most proximal to the outcome in the causal pathway is difficult to measure. For instance, measuring the amount of tar in a person’s lungs is an invasive procedure; measuring the amount of cigarettes a person smokes is much easier in comparison. Therefore, data availability may dictate that we model cigarette smoking rather than lung tar. Such variables are often referred to as proxy variables (variables that are not directly relevant, but serve in place of an unobservable or immeasurable relevant variable).

Using cigarette smoking as a proxy variable for lung tar may be a reasonable approach given that there is no interference on the intermediate variable of lung tar by another exogenous variable (i.e. the medication). However, if there is interference on the intermediate variable in the relationship between the exposure and outcome (i.e. significant use of the medication), then the previously measured relationship between smoking and lung cancer will not apply to this population in the same way.

Now, let’s say that some time has gone by and now this medication has become quite common. A new study measured the relationship between smoking and lung cancer in a study population in which 50% of smokers used the medication. Now, let’s say that we are interested in using the data from that study on the relationship between smoking and lung cancer in a simulation for a different location. However, in the location we wish to model, the medication is not approved at a national level and therefore use of the medication is close to zero. However, since we know that the relationship between smoking and lung cancer as we’ve defined it in this example is affected by the use of this medication, applying the data from this new study to this model location would be inappropriate. Rather, we should use data that measured the relationship between smoking and lung cancer in a study population with a similar exposure to the exogenous variable (medication) on the intermediate variable.

Additional Considerations

Another example of when an intermediate variable might interfere with the relationship between an exposure and outcome is when a given intervention decreases the prevalence of an intermediate variable (that is related to an outcome), but the prevalence of that intermediate variable in a specific location is already zero and therefore cannot be decreased any further. The opposite example of an intervention that increases the prevalence of an intermediate variable that is already 100% prevalent also holds true.

For instance, imagine the example of folic acid supplementation (exposure), which decreases folic acid deficiency (intermediate), which causes neural tube birth defects (outcome). Notably, neural tube birth defects are also caused through other causal pathways such as maternal diabetes. Given that the causal pathway from folic acid fortification–>folic acid deficiency–>neural tube defects is true, we would expect an increase in exposure to folic acid supplementation to decrease neural tube defects. However, the maximum effect of increasing exposure to folic acid supplementation is dependent on the prevalence of the intermediary, folic acid deficiency, in the population. Notably, if folic acid deficiency is zero, increasing folic acid supplementation exposure will have no effect on neural tube defects (there is no folic acid deficiency in the population!). We will need to act on other exposures to reduce neural tube defects in this population, assuming there are other causal pathways for neural tube defects (eg. maternal diabetes)

The impact of interference by intermediate variables between a given exposure and outcome should be carefully considered when designing simulation models. Particularly, special consideration should be given to how a relationship between an exposure and outcome may differ in various populations based on the differing levels of the intermediate variables.

Notably, when the exact mechanism that drives the effect of an exposure on an outcome is not well understood, it is possible that there may be unknown or unmeasured intermediate variables on the causal pathway between the exposure and outcome. In this case, it is important to carefully consider the generalizability of data sources that measure the relationship between the exposure and outcome to the model population to which it will be applied; or in other words, consider key similarities and differences between between the study and model populations that may or may not cause the study data to accurately reflect the situation in the model population. Additionally, limitations of the model should be noted when appropriate.

Effect Modification

A factor \(M\) is said to be an effect modifier if the effect of the exposure \(E\) on disease \(D\) varies for different values of \(M\). Effect modification is sometimes also called interaction. We illustrate this relationship below.

If \(M\) is some dichotomous effect modifier, then \(B\neq C\), and \(A\) does not encompass the entire picture of how \(E\) acts on \(O\). Rather, \(A\) was calculated from some population; for the sake of example, let’s say that \(M=1\) in \(\frac{1}{10}\) of this population. Then we see that \(A\) is tells us about the effect of \(E\) on a new population if and only if the new population also has the same prevalence of \(M\). If we wish to understand how \(E\) operates in some population where \(M\) is prevalent in \(\frac{1}{3}\) of the population, then we would need to know \(B\) and \(C\).

Observe this is in direct contrast to confounding, in which the exposure and confounding factor must not depend on one another to determine the risk.

We note that effect modification is a statistical phenomenon which may or may not reflect a biological phenomenon. However, in the case of epidemiological modeling, following the Bradford-Hill criteria of plausibility, we would hope to be able to explain the effect modification when implementing an effect modifier in a model.

Consider asbestos dust as an exposure for lung cancer. Say that in a cohort study, we find the following:

Death rate per 100,000py: asbestos exposure alone

No Asbestos exposure	66.95
Asbestos exposure	470.85

We might now conclude that the effect of asbestos on lung cancer has a rate ratio for \(470.85/66.95\approx 7.0\). However, when we stratify by smoking, we find the following:

Death rates per 100,000py: asbestos exposure stratified by smoking status

	Non smokers	Smokers
No Asbestos exposure	11.3	122.6
Asbestos exposure	40.1	901.6

This shows us that the rate ratios for the effect of asbestos on lung cancer vary according to smoking status: the rate ratio is \(40.1/11.3\approx 3.5\) for non-smokers and \(901.6/122.6\approx 7.3\) for smokers.

Todo

add citation to Nicole’s textbook. Graphs below were reproduced from http://osctr.ouhsc.edu/sites/default/files/2020-02/Module8PartVNotes.pdf

We include below a graphical representation of a risk outcome stratified by sex, and by age. On the y-axis we have incidence of some outcome such as high blood pressure, and on the x-axis we have an exposure such as obesity.

Todo

Format citations.

Observe that the difference in incidence of high blood pressure, between people from Town A versus Town B, is not modified by the exposure status. Thus the incidence ratio between exposed and unexposed groups, within this population, is not modified by town of residence.

Here, we see that the risk attributable to our exposure is higher in our older group than in our younger group; thus age is an effect modifier for this risk outcome.

Finally, we emphasize that when dealing with a confounding variable, in order to best understand the effects of our exposure, we seek to remove the influence of the confounder. By contrast, if variable B is an effect modifier for exposure A, then this interaction is an important property of the relationship between A and B, and their influence on the disease. Rather than remove, we thus try to capture and describe effect modification in the greatest detail possible. (Cite Nicole’s textbook)

Effect modification in GBD

GBD models estimate globally, and almost all of GBD’s relative risks are used universally across location, sex, age, and time. This means that GBD generally assumes that the study populations from which they calculate their relative risks are applicable universally, without adjustments for the different sexes, locations, or other potential effect modifiers. When using GBD risk factors in a Vivarium model, it is thus important to know what studies GBD used for their relative risk calculation. From these studies it is necessary to consider:

• what the prevalence of various effect modifiers in these populations might have been

• if we believe these are similar enough to the populations we are modeling to use GBD effect sizes

In the case that GBD effect sizes are not generalizeable and we are unable to find studies that supply relative risks and effect sizes stratified by the appropriate effect modifiers, it is also necessary to state the uncertainty that will derive from this lack of information.

Mediation

Definition: Mediation analysis aims to disentangle the effect of an independent variable on an dependent variable explained (indirect effect) or unexplained (direct effect) by a given set of mediators. Rather than a direct causal relationship between the independent variable and the dependent variable, a mediating variable improves understanding the relationship between the independent and dependent variables. The independent variable influences the mediating variable, which in turn influences the dependent variables.

Generic Depiction:

Example:

Direct versus indirect effects: In the example diagram shown above, the indirect effect is the product of path coefficients “1” and “3”. The direct effect is the coefficient “2”. The direct effect measures the extent to which the dependent variable changes when the independent variable increases by one unit and the mediator variable remains unaltered. In contrast, the indirect effect measures the extent to which the dependent variable changes when the independent variable is held fixed and the mediator variable changes by the amount it would have changed had the independent variable increased by one unit. In linear systems, the total effect is equal to the sum of the direct and indirect (2 + 1*3 in the model above). In nonlinear models, the total effect is not generally equal to the sum of the direct and indirect effects, but to a modified combination of the two.

Multiple risk factors: non-independent risk case (aka: mediation). If MF is mediation factor if Risk 2 through Risk 1 for a given cause

\[RR_2 = (RR_2 - 1)(1 - MF_{2/1}) + 1\]

Generalized for multiple pathways of R1 through other RFs

\[RR_i = (RR_i - 1)(1 - \prod_{j = 1}^n (1 - MF_{i/j})) + 1\]

This adjusted or non-mediated RR is then used to calculate a non-mediated PAF, with which we can assume independence across risk factors when aggregating

Here is GBD mediator template which belongs to GBD/risk factors causal criteria section

Causal Inference in the Global Burden of Disease Study

Notably, GBD researchers use an evidence scoring system that is based off of a subset of the Bradford Hill Criteria to evaluate the quality of evidence regarding causal relationships between risk-outcome pairs in GBD. Specifically, before computing the relative risks for a GBD risk factor, GBD researchers evaluate the risk of bias among individual studies that investigate the relationship between a risk-outcome pair. Then, GBD researchers additionally evaluate the strength (as a direct result of the relative risk curve they compute), consistency (through evaluating between study heterogeneity), and dose-response (through the shape of the relative risk curve) for the computed relative risks for a given risk factor. Using these criteria, GBD researchers create a quantitive quality of evidence score for each risk-outcome pair in GBD.

Note

The formal evidence scoring system is planned to be used in GBD 2020 and was not used in this systematic way for previous GBD rounds.

Additional, this evaluation of the epidemiological evidence to support a causal relationship between a risk-outcome pair is part of a large process that GBD uses to select risk-outcome pairs to model, which includes an evaluation of the importance of the risk factor to the outcome, data availability, and generalizability.

Specifically, GBD researchers evaluate the risk of bias within individual studies based on the following characteristics:

1. Representativeness of the study population

2. Exposure measurement

1. Individual versus population

2. Objective versus self-report

3. Multiple prospective versus baseline prospective versus retrospective

3. Outcome measurement

1. Death certificatie/physician diagnosis/medical records versus self-report

2. Blind outcome assessment versus not

4. Reverse causation: low, medium, high

5. Control for confounding

1. Randomized controlled trial

2. Age, sex, tobacco, income, education, other critical determinants for a specific outcome not on the causal pathway

3. Age, sex, tobacco, other critical determininants for a specific outcome not on the causal pathway

4. Age, sex

6. Selection bias

1. High follow-up (95%), not opportunity for selection

2. Moderate follow-up (85-95%), limited opportunity for selection

3. Low follow-up (<85%), considerable opportunity for selection

Parameters related to evidence quality are then accounted for in the assessment of the relationship of the risk-outcome pair through MR-BRT analyses.

Note

This information was obtained from a science seminar presented by Ryan Barber and Chris Murray on March 11, 2020; a recording is available here. Documentation for GBD’s evidence scoring system is available here.