Causal Models and Metaphysics – two interesting papers by Jenn McDonald

These look fun, by Jenn McDonald:

Causal Models and Metaphysics – Part 1: Using Causal Models

“This paper provides a general introduction to the use of causal models in the metaphysics of causation, specifically structural equation models and directed acyclic graphs. It reviews the formal framework, lays out a method of interpretation capable of representing different underlying metaphysical relations, and describes the use of these models in analyzing causation.”

Causal Models and Metaphysics – Part 2: Interpreting Causal Models

“This paper addresses the question of what constitutes an apt interpreted model for the purpose of analyzing causation. I first collect universally adopted aptness principles into a basic account, flagging open questions and choice points along the way. I then explore various additional aptness principles that have been proposed in the literature but have not been widely adopted, the motivations behind their proposals, and the concerns with each that stand in the way of universal adoption. I conclude that the remaining work of articulating aptness for a SEM analysis of causation is tied up with issue to do with modality, ontology, and mereology. Continuing this work is therefore likely to shed light on the relationship between these areas and causation more generally.”

 

 

TBE QEDs

‘In TBE [theory-based evaluation] practice […] theory as represented is not specific enough to support causal conclusions in inference […]. For example, in contribution analysis “causal assumptions” refer to a “causal package” consisting of the program intervention and a set of contextual conditions that together may explain an observed change in the outcome […]. In realist evaluation, the causal mechanisms that are triggered by the intervention are specified in “configuration” with their context and the outcome. Often, however, the causal structure of the configuration is not clear […]. Moreover, the main TBE approaches to inference do not have standard practices, conventions, for treating bias in evidence […].

‘TBE practitioners may borrow from other methods to test theoretical assumptions […]. Sometimes TBE employs regression analysis or quasi-experimental propensity score matching in inference (our running example in this article of an actual TBE program evaluation does so).’

Schmidt, R. (2024). A graphical method for causal program attribution in theory-based evaluation. Evaluation, online first.

 

Data alone can’t determine causal structure

Suppose we find that the probability of a successful programme outcome (out) depends on treatment (treat) and mediator (med) as per the Bayes network depicted in part 1 of the figure below. Suppose also that there are no other unmeasured variables. This model defines \(P(\mathit{out} | \mathit{treat}, \mathit{med})\), \(P(\mathit{med} | \mathit{treat})\), and \(P(\mathit{treat})\). The arrows denote these probabilistic relationships.

Interpreting the arrows as causal relations, then all six models above are consistent with the conditional probabilities. Model 2 says that treatment and outcome are associated with each other because the mediator is a common cause. Model 3 says that the outcome causes treatment assignment. Model 4 says that the treatment causes mediator and outcome; however, outcome causes mediator. And so on. These six models are all members of the same Markov equivalence class (see Verma & Pearl, 1990).

We need something beyond the data and statistical assocations to distinguish between them: theory. Some of the theory might be trivial, e.g., that the outcome followed treatment and can’t have caused the treatment because we have ruled out time travel.

References

Verma, T., & Pearl, J. (1990). Equivalence and synthesis of causal models. Proceedings of the Sixth Annual Conference on Uncertainty in Artificial Intelligence, 255–270.

Actual causes: two examples using the updated Halpern-Pearl definition

Halpern (2015) provides three variants of the Halpern-Pearl definitions of actual causation. I’m trying to get my head around the formalism, which is elegant, concise, and precise, but tedious to use in practice, so I wrote an R script to do the sums. This blog post is not self-contained – you will need to read the original paper for an introduction to the model. However, it works through two examples, which may help if you’re also struggling with the paper.

The second (“updated”) definition of an actual cause asserts that \(\vec{A} = \vec{a}\) is a cause of \(\varphi\) in \((M,\vec{u})\) iff the following conditions hold:

AC1 \((M,\vec{u}) \models (\vec{A} =\vec{a}) \land \varphi\).

This says, if \(\vec{A} = \vec{a}\) is an actual cause of \(\varphi\) then they both hold in the actual world, \((M,\vec{u})\). Note, for this condition, we are just having a look at the model and not doing anything to it.

AC2 There is a partition of the endogenous variables in \(M\) into \(\vec{Z} \supseteq \vec{X}\) and \(\vec{W}\) and there are settings \(\vec{x’}\) and \(\vec{w}\) such that

(a) \((M,\vec{u}) \models [ \vec{X} \leftarrow \vec{x’}, \vec{W} \leftarrow \vec{w}] \neg \varphi\).

So, we’re trying to show that undoing the cause, i.e., setting \(\vec{X}\) to \(\vec{x’} \ne \vec{x}\), prevents the effect. We are allowed to modify \(\vec{W}\) however we want to show this, whilst leaving \(\vec{Z}-\vec{X}\) free to do whatever the model tells these variables to do.

(b) If \((M,\vec{u}) \models \vec{Z} = \vec{z^{\star}}\), for some \(\vec{z^{\star}}\), then for all \(\vec{W’} \subseteq \vec{W}\) and \(\vec{Z’} \subseteq \vec{Z}-\vec{X}\),
\((M,\vec{u}) \models [ \vec{X} \leftarrow \vec{x}, \vec{W’} \leftarrow \vec{w’}, \vec{Z’} \leftarrow \vec{z^{\star}}] \varphi\).

This says, trigger the cause (unlike AC1, we aren’t just looking to see if it holds) and check whether it leads to the effect under all subsets of \(\vec{Z}\) (as per actual world) that aren’t \(\vec{X}\) and all subsets of the modified \(\vec{W}\) that we found for AC2(a). Note how we are setting \(\vec{Z}\) for those subsets, rather than just observing it.

AC3 There is no \(\vec{A’} \subset \vec{A}\) such that \(\vec{A’} = \vec{a’}\) satisfies AC1 and AC2.

This says, there’s no superfluous stuff in \(\vec{A}\). You taking a painkiller and waving a magic wand doesn’t cause your headache to disappear, under AC3, if the painkiller works without the wand.

Example 1: an (actual) actual cause

Let’s give it a go with an overdetermined scenario (lightly edited from Halpern) that Alice and Bob both lob bricks at a glasshouse and smash the glass. Define

\(\mathit{AliceThrow} = 1\)
\(\mathit{BobThrow} = 1\)
\(\mathit{GlassBreaks} = \mathit{max}(\mathit{AliceThrow},\mathit{BobThrow})\)

So, if either Alice or Bob (or both) hit the glasshouse, then the glass breaks. Strictly speaking, I should have setup one or more exogenous variables, \(\vec{u}\), that define the context and then defined \(\mathit{AliceThrow}\) and \(\mathit{BobThrow}\) in terms of \(\vec{u}\), but it works fine to skip that step as I have here since I’m holding \(\vec{u}\) constant anyway.

Is \(\mathit{AliceThrow} = 1\) an actual cause of \(\mathit{GlassBreaks} = 1\)?

AC1 holds since \((M,\vec{u}) \models \mathit{AliceThrow} = 1 \land \mathit{GlassBreaks} = 1\). The first conjunct comes directly from one of the model equations and none of the functions change it. Spelling out the second conjunct,

\(\mathit{GlassBreaks} = \mathit{max}(\mathit{AliceThrow},\mathit{BobThrow})\)
\(= \mathit{max}(1, 1)\)
\(= 1\)

For AC2, we need to find a partition of the endogenous variables such that AC2(a) and AC2(b) hold. Try \(\vec{Z} = \{ \mathit{AliceThrow}, \mathit{GlassBreaks} \}\) and \(\vec{W}= \{ \mathit{BobThrow} \}\).

AC2(a) holds since \((M,\vec{u}) \models [ \mathit{AliceThrow} \leftarrow 0, \mathit{BobThrow} \leftarrow 0] \mathit{GlassBreaks} = 0\).

For AC2(b), we begin with \(\vec{Z} = \{ \mathit{AliceThrow}, \mathit{GlassBreaks} \}\) and the settings as per the unchanged model, so

\((M,\vec{u}) \models \mathit{AliceThrow} = 1 \land \mathit{GlassBreaks} = 1\).

We need to check that for all \(\vec{W’} \subseteq \vec{W}\) and \(\vec{Z’} \subseteq \vec{Z}-\vec{X}\),
\((M,\vec{u}) \models [ \vec{X} \leftarrow \vec{x}, \vec{W’} \leftarrow \vec{w’}, \vec{Z’} \leftarrow \vec{z^{\star}}] \varphi\).

Here are the combinations and \(\varphi \equiv \mathit{GlassBreaks} = 1\) holds for all of them:

\((M,\vec{u}) \models [ \mathit{AliceThrow} \leftarrow 1, \mathit{GlassBreaks} \leftarrow 1, \mathit{BobThrow} \leftarrow 0 ] \varphi\)
\((M,\vec{u}) \models [ \mathit{AliceThrow} \leftarrow 1, \mathit{BobThrow} \leftarrow 0 ] \varphi\)
\((M,\vec{u}) \models [ \mathit{AliceThrow} \leftarrow 1, \mathit{GlassBreaks} \leftarrow 1 ] \varphi\)
\((M,\vec{u}) \models [ \mathit{AliceThrow} \leftarrow 1 ] \varphi \)

(The third was rather trivially true; however, as far as I understand, has to be checked given the definition.)

AC3 is easy since the cause only has one variable, so there’s nothing superfluous.

Example 2: not an actual cause

Now let’s try an example that isn’t an actual cause: the glass breaking causes Alice to throw the brick. It’s obviously false; however, it wasn’t clear to me exactly where it would fail until I worked through this…

AC1 holds since in the actual world, \(\mathit{GlassBreaks} = 1\) and \(\mathit{AliceThrow} = 1\) hold.

Examining the function defintions, they don’t provide a way to link \(\mathit{AliceThrow}\) to a change in \(\mathit{GlassBreaks}\), so the only apparent way to do so is through \(\vec{W}\). Therefore, use the partition \(\vec{W} = \{\mathit{AliceThrow}\}\) and \(\vec{Z} = \{\mathit{GlassBreaks}, \mathit{BobThrow}\}\).

Now for AC2(a), we can easily get \(\mathit{AliceThrow} = 0\) as required, since we can do what we like with \(\vec{W}\). It doesn’t help when we move onto AC2(b) since we have to hold \(\mathit{AliceThrow} = 0\), which is the negation of what we want. The same is the case for the other partition including \(\mathit{AliceThrow}\) in \(\vec{W}\), i.e., \(\vec{W} = \{ \mathit{AliceThrow}, \mathit{BobThrow} \}\).

So, the broken glass does not cause Alice to throw a brick. The setup we needed to get through AC2(a) set us up to fail AC2(b).

References

Halpern, J. Y. (2015). A Modification of the Halpern-Pearl Definition of Causality. Proceedings of the Twenty-Fourth International Joint Conference on Artificial Intelligence (IJCAI 2015), 3022–3033.

See also this companion blog post.

What is a counterfactual?

What’s a counterfactual? Philosophers love the example, “If Oswald hadn’t killed Kennedy, someone else would have”. More generally, Y would be y had X been x in situation U = u (Judea Pearl’s, 2011, rendering).

References

Pearl, J. (2011). The structural theory of causation. In P. McKay Illari, F. Russo, & J. Williamson (Eds.), Causality in the Sciences (pp. 697–727). Oxford University Press.

What is Theory-Based Evaluation, really?

It is a cliché that randomised controlled trials (RCTs) are the gold standard if you want to evaluate a social policy or intervention and quasi-experimental designs (QEDs) are presumably the silver standard. But often it is not possible to use either, especially for complex policies. Theory-Based Evaluation is an alternative that has been around for a few decades, but what exactly is it?

In this post I will sketch out what some key texts say about Theory-Based Evaluation; explore one approach, contribution analysis; and conclude with discussion of an approach to assessing evidence in contribution analyses (and a range of other approaches) using Bayes’ rule.

theory (lowercase)

Let’s get the obvious out of the way. All research, evaluation included, is “theory-based” by necessity, even if an RCT is involved. Outcome measures and interviews alone cannot tell us what is going on; some sort of theory (or story, account, narrative, …) – however flimsy or implicit – is needed to design an evaluation and interpret what the data means.

If you are evaluating a psychological therapy, then you probably assume that attending sessions exposes therapy clients to something that is likely to be helpful. You might make assumptions about the importance of the therapeutic relationship to clients’ openness, of any homework activities carried out between sessions, etc. RCTs can include statistical mediation tests to determine whether the various things that happen in therapy actually explain any difference in outcome between a therapy and comparison group (e.g., Freeman et al., 2015).

It is great if a theory makes accurate predictions, but theories are underdetermined by evidence, so this cannot be the only criterion for preferring one theory’s explanation over another (Stanford, 2017) – again, even if you have an effect size from an RCT. Lots of theories will be compatible with any RCT’s results. To see this, try a particular social science RCT and think hard about what might be going on in the intervention group beyond what the intervention developers have explicitly intended.

In addition to accuracy, Kuhn (1977) suggests that a good theory should be consistent with itself and other relevant theories; have broad scope; bring “order to phenomena that in its absence would be individually isolated”; and it should produce novel predictions beyond current observations. There are no obvious formal tests for these properties, especially where theories are expressed in ordinary language and box-and-arrow diagrams.

Theory-Based Evaluation (title case)

Theory-Based Evaluation is a particular genre of evaluation that includes realist evaluation and contribution analysis. According the UK’s government’s Magenta Book (HM Treasury, 2020, p. 43), Theory-Based methods of evaluation

“can be used to investigate net impacts by exploring the causal chains thought to bring about change by an intervention. However, they do not provide precise estimates of effect sizes.”

The Magenta Book acknowledges (p. 43) that “All evaluation methods can be considered and used as part of a [Theory-Based] approach”; however, Figure 3.1 (p. 47) is clear. If you can “compare groups affected and not affected by the intervention”, you should go for experiments or quasi-experiments; otherwise, Theory-Based methods are required.

The route to Theory-Based Evaluation according to the Magenta Book.

Theory-Based Evaluation attempts to draw causal conclusions about a programme’s effectiveness in the absence of any comparison group. If a quasi-experimental design (QED) or randomised controlled trial (RCT) were added to an evaluation, it would cease to be Theory-Based Evaluation, as the title case term is used.

Example: Contribution analysis

Contribution analysis is an approach to Theory-Based Evaluation developed by John Mayne (28 November 1943 – 18 December 2020). Mayne was originally concerned with how to use monitoring data to decide whether social programmes actually worked when quasi-experimental approaches were not feasible (Mayne, 2001), but the approach evolved to have broader scope.

According to a recent summary (Mayne, 2019), contribution analysis consists of six steps (and an optional loop):

Step 1: Set out the specific cause-effect questions to be addressed.

Step 2: Develop robust theories of change for the intervention and its pathways.

Step 3: Gather the existing evidence on the components of the theory of change model of causality: (i) the results achieved and (ii) the causal link assumptions realized.

Step 4: Assemble and assess the resulting contribution claim, and the challenges to it.

Step 5: Seek out additional evidence to strengthen the contribution claim.

Step 6: Revise and strengthen the contribution claim.

Step 7: Return to Step 4 if necessary.

Here is a diagrammatic depiction of the kind of theory of change that could be plugged in at Step 2 (Mayne, 2015, p. 132), which illustrates the cause-effect links an evaluation would aim to evaluate.

In this example, mothers are thought to learn from training sessions and materials, which then persuades them to adopt new feeding practices. This leads to children having more nutritious diets. The theory is surrounded by various contextual factors such as food prices. (See also Mayne, 2017, for a version of this that includes ideas from the COM-B model of behaviour.)

Step 4 is key. It requires evaluators to “Assemble and assess the resulting contribution claim”. How are we to carry out that assessment? Mayne (2001, p. 14) suggests some questions to ask:

“How credible is the story? Do reasonable people agree with the story? Does the pattern of results observed validate the results chain? Where are the main weaknesses in the story?”

For me, the most credible stories would include experimental or quasi-experimental tests, with mediation analysis of key hypothesised mechanisms, and qualitative detective work to get a sense of what’s going on beyond the statistical associations. But the quant part of that would lift us out of the Theory-Based Evaluation wing of the Magenta Book flowchart. In general, plausibility will be determined outside contribution analysis in, e.g., quality criteria for whatever methods for data collection and analysis were used. Contribution analysis says remarkably little on this key step.

Although contribution analysis is intended to fill a gap where no comparison group is available, Mayne (2001, p. 18) suggests that further data might be collected to help rule out alternative explanations of outcomes, e.g., from surveys, field visits, or focus groups. He also suggests reviewing relevant meta-analyses, which could (I presume) include QED and RCT evidence.

It is not clear to me what the underlying theory of causation is in contribution analysis. It is clear what it is not (Mayne, 2019, pp. 173–4):

“In many situations a counterfactual perspective on causality—which is the traditional evaluation perspective—is unlikely to be useful; experimental designs are often neither feasible nor practical…”

“[Contribution analysis] uses a stepwise (generative) not a counterfactual approach to causality.”

(We will explore counterfactuals below.) I can guess what this generative approach could be, but Mayne does not provide precise definitions. It clearly isn’t the idea from generative social science in which causation is defined in terms of computer simulations (Epstein, 1999).

One way to think about it might be in terms of mechanisms: “entities and activities organized in such a way that they are responsible for the phenomenon” (Illari & Williamson, 2011, p. 120). We could make this precise by modelling the mechanisms using causal Bayesian networks such that variables (nodes in a network) represent the probability of activities occurring, conditional on temporally earlier activities having occurred – basically, a chain of probabilistic if-thens.

Why do people get vaccinated for Covid-19? Here is the beginning of a (generative?) if-then theory:

  1. If you learned about vaccines in school and believed what you learned and are exposed to an advert for Covid-19 jab and are invited by text message to book an appointment for one, then (with a certain probability) you use your phone to book an appointment.
  2. If you have booked an appointment, then (with a certain probability) you travel to the vaccine centre in time to attend the appointment.
  3. If you attend the appointment, then (with a certain probability) you are asked to join a queue.

… and so on …

In a picture:

Causal directed acyclic graph (DAG) showing how being exposed to a text message invitation to receive a vaccine may lead to protection against Covid-19

This does not explain how or why the various entities (people, phones, etc.) and activities (doing stuff like getting the bus as a result of beliefs and desires) are organised as they are, just the temporal order in which they are organised and dependencies between them. Maybe this suffices.

What are counterfactual approaches?

Counterfactual impact evaluation usually refers to quantitative approaches to estimate average differences as understood in a potential outcomes framework (or generalisations thereof). The key counterfactual is something like:

“If the beneficiaries had not taken part in programme activities, then they would not have had the outcomes they realised.”

Logicians have long worried how to determine the truth of counterfactuals, “if A had been true, B.” One approach, due to Stalnaker (1968), proposes that you:

  1. Start with a model representing your beliefs about the factual situation where A is false. This model must have enough structure so that tweaking it could lead to different conclusions (causal Bayesian networks have been proposed; Pearl, 2013).
  2. Add A to your belief model.
  3. Modify the belief model in a minimal way to remove contradictions introduced by adding A.
  4. Determine the truth of B in that revised belief model.

This broader conception of counterfactual seems compatible with any kind of evaluation, contribution analysis included. White (2010, p. 157) offered a helpful intervention, using the example of a pre-post design where the same outcome measure is used before and after an intervention:

“… having no comparison group is not the same as having no counterfactual. There is a very simple counterfactual: what would [the outcomes] have been in the absence of the intervention? The counterfactual is that it would have remained […] the same as before the intervention.”

The counterfactual is untested and could be false – regression to the mean would scupper it in many cases. But it can be stated and used in an evaluation. I think Stalnaker’s approach is a handy mental trick for thinking through the implications of evidence and producing alternative explanations.

Cook (2000) offers seven reasons why Theory-Based Evaluation cannot “provide the valid conclusions about a program’s causal effects that have been promised.” I think from those seven, two are key: (i) it is usually too difficult to produce a theory of change that is comprehensive enough for the task and (ii) the counterfactual remains theoretical – in the arm-chair, untested sense of theoretical – so it is too difficult to judge what would have happened in the absence of the programme being evaluated. Instead, Cook proposes including more theory in comparison group evaluations.

Bayesian contribution tracing

Contribution analysis has been supplemented with a Bayesian variant of process tracing (Befani & Mayne, 2014; Befani & Stedman-Bryce, 2017; see also Fairfield & Charman, 2017, for a clear introduction to Bayesian process tracing more generally).

The idea is that you produce (often subjective) probabilities of observing particular (usually qualitative) evidence under your hypothesised causal mechanism and under one or more alternative hypotheses. These probabilities and prior probabilities for your competing hypotheses can then be plugged into Bayes’ rule when evidence is observed.

Suppose you have two competing hypotheses: a particular programme led to change versus pre-existing systems. You may begin by assigning them equal probability, 0.5 and 0.5. If relevant evidence is observed, then Bayes’ rule will shift the probabilities so that one becomes more probable than the other.

Process tracers often cite Van Evera’s (1997) tests such as the hoop test and smoking gun. I find definitions of these challenging to remember so one thing I like about the Bayesian approach is that you can think instead of specificity and sensitivity of evidence, by analogy with (e.g., medical) diagnostic tests. A good test of a causal mechanism is sensitive, in the sense that there is a high probability of observing the relevant evidence if your causal theory is accurate. A good test is also specific, meaning that the evidence is unlikely to be observed if any alternative theory is true. See below for a table (lighted edited from Befani & Mayne, 2014, p. 24) showing the conditional probabilities of evidence for each of Van Evera’s tests given a hypothesis and alternative explanation.

Van Evera test
if Eᵢ is observed
P(Eᵢ | Hyp) P(Eᵢ | Alt)
Fails hoop test Low
Passes smoking gun Low
Doubly-decisive test High Low
Straw-in-the-wind test High High

Let’s take the hoop test. This applies to evidence which is unlikely if your preferred hypothesis were true. So if you observe that evidence, the hoop test fails. The test is agnostic about the probability under the alternative hypothesis. Straw-in-the-wind is hopeless for distinguishing between your two hypotheses, but could suggest that neither holds if the test fails. The double-decisive test has high sensitivity and high specificity, so provides strong evidence for your hypothesis if it passes.

The arithmetic is straightforward if you stick to discrete multinomial variables and use software for conditional independence networks. Eliciting the subjective probabilities for each source of evidence, conditional on each hypothesis, may be less straightforward.

Conclusions

I am with Cook (2000) and others who favour a broader conception of “theory-based” and suggest that better theories should be tested in quantitative comparison studies. However, it is clear that it is not always possible to find a comparison group – colleagues and I have had to make do without (e.g., Fugard et al., 2015). Using Theory-Based Evaluation in practice reminds me of jury service: a team are guided through thick folders of evidence, revisiting several key sections that are particularly relevant, and work hard to reach the best conclusion they can with what they know. There is no convenient effect size to consult, just a shared (to some extent) and informal idea of what intuitively feels more or less plausible (and lengthy discussion where there is disagreement). To my mind, when quantitative comparison approaches are not possible, Bayesian approaches to assessing qualitative evidence are the most compelling way to synthesise qualitative evidence of causal impact and make transparent how this synthesis was done.

Finally, it seems to me that the Theory-Based Evaluation category is poorly named. Better might be, Assumption-Based Counterfactual approaches. Then RCTs and QEDs are Comparison-Group Counterfactual approaches. Both are types of theory-based evaluation and both use counterfactuals; it’s just that approaches using comparison groups gather quantitative evidence to test the counterfactual. However, the term doesn’t quite work since RCTs and QEDs rely on assumptions too… Further theorising needed.

Edited to add: Reichardt’s (2022), The Counterfactual Definition of a Program Effect, is a very promising addition to the literature and, I think, offers a clear way out of the theory-based versus non-theory-based and counterfactual versus not-counterfactual false dichotomies. I’ve blogged about it here.

(If you found this post interesting, please do say hello and let me know!)

References

Befani, B., & Mayne, J. (2014). Process Tracing and Contribution Analysis: A Combined Approach to Generative Causal Inference for Impact Evaluation. IDS Bulletin, 45(6), 17–36.

Befani, B., & Stedman-Bryce, G. (2017). Process Tracing and Bayesian Updating for impact evaluation. Evaluation, 23(1), 42–60.

Cook, T. D. (2000). The false choice between theory-based evaluation and experimentation. In A. Petrosino, P. J. Rogers, T. A. Huebner, & T. A. Hacsi (Eds.), New directions in evaluation: Program Theory in Evaluation: Challenges and Opportunities (pp. 27–34). Jossey-Bass.

Epstein, J. M. (1999). Agent-based computational models and generative social science. Complexity, 4(5), 41–60.

Fairfield, T., & Charman, A. E. (2017). Explicit bayesian analysis for process tracing: Guidelines, opportunities, and caveats. Political Analysis, 25(3), 363–380.

Freeman, D., Dunn, G., Startup, H., Pugh, K., Cordwell, J., Mander, H., Černis, E., Wingham, G., Shirvell, K., & Kingdon, D. (2015). Effects of cognitive behaviour therapy for worry on persecutory delusions in patients with psychosis (WIT): a parallel, single-blind, randomised controlled trial with a mediation analysis. The Lancet Psychiatry, 2(4), 305–313.

Fugard, A. J. B., Stapley, E., Ford, T., Law, D., Wolpert, M. & York, A. (2015). Analysing and reporting UK CAMHS outcomes: an application of funnel plotsChild and Adolescent Mental Health, 20, 155–162.

HM Treasury. (2020). Magenta Book.

Illari, P. M., & Williamson, J. (2011). What is a mechanism? Thinking about mechanisms across the sciences. European Journal for Philosophy of Science, 2(1), 119–135.

Kuhn, T. S. (1977). Objectivity, Value Judgment, and Theory Choice. In The Essential Tension: Selected Studies in Scientific Tradition and Change (pp. 320–339). The University of Chicago Press.

Mayne, J. (2001). Addressing attribution through contribution analysis: using performance measures sensibly. The Canadian Journal of Program Evaluation, 16(1), 1–24.

Mayne, J. (2015). Useful theory of change models. Canadian Journal of Program Evaluation, 30(2), 119–142.

Mayne, J. (2017). Theory of change analysis: Building robust theories of change. Canadian Journal of Program Evaluation, 32(2), 155–173.

Mayne, J. (2019). Revisiting contribution analysis. Canadian Journal of Program Evaluation, 34(2), 171–191.

Pearl, J. (2013). Structural counterfactuals: A brief introduction. Cognitive Science, 37(6), 977–985.

Stalnaker, R. C. (1968). A Theory of Conditionals. In Ifs (pp. 41–55). Basil Blackwell Publisher.

Stanford, K. (2017). Underdetermination of Scientific Theory. In E. N. Zalta (Ed.), The Stanford Encyclopedia of Philosophy.

Van Evera, S. (1997). Guide to Methods for Students of Political Science. New York, NY: Cornell University Press.

White, H. (2010). A contribution to current debates in impact evaluation. Evaluation, 16(2), 153–164.

Use of directed acyclic graphs (DAGs) to identify confounders in applied health research: review and recommendations

Neat paper by Tennant, P. W. G. et al. (2020): Use of directed acyclic graphs (DAGs) to identify confounders in applied health research: review and recommendations in the International Journal of Epidemiology.

Picture

Recommendations from the paper

  1. The focal relationship(s) and estimand(s) of interest should be stated in the study aims
  2. The DAG(s) for each focal relationship and estimand of interest should be available
  3. DAGs should include all relevant variables, including those where direct measurements are unavailable
  4. Variables should be visually arranged so that all constituent arcs flow in the same direction
  5. Arcs should generally be assumed to exist between any two variables
  6. The DAG-implied adjustment set(s) for the estimand(s) of interest should be clearly stated
  7. The estimate(s) obtained from using the unmodified DAG-implied adjustment set(s)—or nearest approximation thereof—should be reported
  8. Alternative adjustment set(s) should be justified and their estimate(s) reported separately