causal hypothesis research definition

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Causal research: definition, examples and how to use it.

16 min read Causal research enables market researchers to predict hypothetical occurrences & outcomes while improving existing strategies. Discover how this research can decrease employee retention & increase customer success for your business.

What is causal research?

Causal research, also known as explanatory research or causal-comparative research, identifies the extent and nature of cause-and-effect relationships between two or more variables.

It’s often used by companies to determine the impact of changes in products, features, or services process on critical company metrics. Some examples:

• How does rebranding of a product influence intent to purchase?
• How would expansion to a new market segment affect projected sales?
• What would be the impact of a price increase or decrease on customer loyalty?

To maintain the accuracy of causal research, ‘confounding variables’ or influences — e.g. those that could distort the results — are controlled. This is done either by keeping them constant in the creation of data, or by using statistical methods. These variables are identified before the start of the research experiment.

As well as the above, research teams will outline several other variables and principles in causal research:

• Independent variables

The variables that may cause direct changes in another variable. For example, the effect of truancy on a student’s grade point average. The independent variable is therefore class attendance.

• Control variables

These are the components that remain unchanged during the experiment so researchers can better understand what conditions create a cause-and-effect relationship.  

This describes the cause-and-effect relationship. When researchers find causation (or the cause), they’ve conducted all the processes necessary to prove it exists.

• Correlation

Any relationship between two variables in the experiment. It’s important to note that correlation doesn’t automatically mean causation. Researchers will typically establish correlation before proving cause-and-effect.

• Experimental design

Researchers use experimental design to define the parameters of the experiment — e.g. categorizing participants into different groups.

• Dependent variables

These are measurable variables that may change or are influenced by the independent variable. For example, in an experiment about whether or not terrain influences running speed, your dependent variable is the terrain.  

Why is causal research useful?

It’s useful because it enables market researchers to predict hypothetical occurrences and outcomes while improving existing strategies. This allows businesses to create plans that benefit the company. It’s also a great research method because researchers can immediately see how variables affect each other and under what circumstances.

Also, once the first experiment has been completed, researchers can use the learnings from the analysis to repeat the experiment or apply the findings to other scenarios. Because of this, it’s widely used to help understand the impact of changes in internal or commercial strategy to the business bottom line.

Some examples include:

• Understanding how overall training levels are improved by introducing new courses
• Examining which variations in wording make potential customers more interested in buying a product
• Testing a market’s response to a brand-new line of products and/or services

So, how does causal research compare and differ from other research types?

Well, there are a few research types that are used to find answers to some of the examples above:

1. Exploratory research

As its name suggests, exploratory research involves assessing a situation (or situations) where the problem isn’t clear. Through this approach, researchers can test different avenues and ideas to establish facts and gain a better understanding.

Researchers can also use it to first navigate a topic and identify which variables are important. Because no area is off-limits, the research is flexible and adapts to the investigations as it progresses.

Finally, this approach is unstructured and often involves gathering qualitative data, giving the researcher freedom to progress the research according to their thoughts and assessment. However, this may make results susceptible to researcher bias and may limit the extent to which a topic is explored.

2. Descriptive research

Descriptive research is all about describing the characteristics of the population, phenomenon or scenario studied. It focuses more on the “what” of the research subject than the “why”.

For example, a clothing brand wants to understand the fashion purchasing trends amongst buyers in California — so they conduct a demographic survey of the region, gather population data and then run descriptive research. The study will help them to uncover purchasing patterns amongst fashion buyers in California, but not necessarily why those patterns exist.

As the research happens in a natural setting, variables can cross-contaminate other variables, making it harder to isolate cause and effect relationships. Therefore, further research will be required if more causal information is needed.

Get started on your market research journey with CoreXM

How is causal research different from the other two methods above?

Well, causal research looks at what variables are involved in a problem and ‘why’ they act a certain way. As the experiment takes place in a controlled setting (thanks to controlled variables) it’s easier to identify cause-and-effect amongst variables.

Furthermore, researchers can carry out causal research at any stage in the process, though it’s usually carried out in the later stages once more is known about a particular topic or situation.

Finally, compared to the other two methods, causal research is more structured, and researchers can combine it with exploratory and descriptive research to assist with research goals.

Summary of three research types

What are the advantages of causal research?

• Improve experiences

By understanding which variables have positive impacts on target variables (like sales revenue or customer loyalty), businesses can improve their processes, return on investment, and the experiences they offer customers and employees.

• Help companies improve internally

By conducting causal research, management can make informed decisions about improving their employee experience and internal operations. For example, understanding which variables led to an increase in staff turnover.

• Repeat experiments to enhance reliability and accuracy of results

When variables are identified, researchers can replicate cause-and-effect with ease, providing them with reliable data and results to draw insights from.

• Test out new theories or ideas

If causal research is able to pinpoint the exact outcome of mixing together different variables, research teams have the ability to test out ideas in the same way to create viable proof of concepts.

• Fix issues quickly

Once an undesirable effect’s cause is identified, researchers and management can take action to reduce the impact of it or remove it entirely, resulting in better outcomes.

What are the disadvantages of causal research?

• Provides information to competitors

If you plan to publish your research, it provides information about your plans to your competitors. For example, they might use your research outcomes to identify what you are up to and enter the market before you.

• Difficult to administer

Causal research is often difficult to administer because it’s not possible to control the effects of extraneous variables.

• Time and money constraints

Budgetary and time constraints can make this type of research expensive to conduct and repeat. Also, if an initial attempt doesn’t provide a cause and effect relationship, the ROI is wasted and could impact the appetite for future repeat experiments.

• Requires additional research to ensure validity

You can’t rely on just the outcomes of causal research as it’s inaccurate. It’s best to conduct other types of research alongside it to confirm its output.

• Trouble establishing cause and effect

Researchers might identify that two variables are connected, but struggle to determine which is the cause and which variable is the effect.

• Risk of contamination

There’s always the risk that people outside your market or area of study could affect the results of your research. For example, if you’re conducting a retail store study, shoppers outside your ‘test parameters’ shop at your store and skew the results.

How can you use causal research effectively?

To better highlight how you can use causal research across functions or markets, here are a few examples:

Market and advertising research

A company might want to know if their new advertising campaign or marketing campaign is having a positive impact. So, their research team can carry out a causal research project to see which variables cause a positive or negative effect on the campaign.

For example, a cold-weather apparel company in a winter ski-resort town may see an increase in sales generated after a targeted campaign to skiers. To see if one caused the other, the research team could set up a duplicate experiment to see if the same campaign would generate sales from non-skiers. If the results reduce or change, then it’s likely that the campaign had a direct effect on skiers to encourage them to purchase products.

Improving customer experiences and loyalty levels

Customers enjoy shopping with brands that align with their own values, and they’re more likely to buy and present the brand positively to other potential shoppers as a result. So, it’s in your best interest to deliver great experiences and retain your customers.

For example, the Harvard Business Review found that an increase in customer retention rates by 5% increased profits by 25% to 95%. But let’s say you want to increase your own, how can you identify which variables contribute to it?Using causal research, you can test hypotheses about which processes, strategies or changes influence customer retention. For example, is it the streamlined checkout? What about the personalized product suggestions? Or maybe it was a new solution that solved their problem? Causal research will help you find out.

Discover how to use analytics to improve customer retention.

Improving problematic employee turnover rates

If your company has a high attrition rate, causal research can help you narrow down the variables or reasons which have the greatest impact on people leaving. This allows you to prioritize your efforts on tackling the issues in the right order, for the best positive outcomes.

For example, through causal research, you might find that employee dissatisfaction due to a lack of communication and transparency from upper management leads to poor morale, which in turn influences employee retention.

To rectify the problem, you could implement a routine feedback loop or session that enables your people to talk to your company’s C-level executives so that they feel heard and understood.

How to conduct causal research first steps to getting started are:

1. Define the purpose of your research

What questions do you have? What do you expect to come out of your research? Think about which variables you need to test out the theory.

2. Pick a random sampling if participants are needed

Using a technology solution to support your sampling, like a database, can help you define who you want your target audience to be, and how random or representative they should be.

3. Set up the controlled experiment

Once you’ve defined which variables you’d like to measure to see if they interact, think about how best to set up the experiment. This could be in-person or in-house via interviews, or it could be done remotely using online surveys.

4. Carry out the experiment

Make sure to keep all irrelevant variables the same, and only change the causal variable (the one that causes the effect) to gather the correct data. Depending on your method, you could be collecting qualitative or quantitative data, so make sure you note your findings across each regularly.

5. Analyze your findings

Either manually or using technology, analyze your data to see if any trends, patterns or correlations emerge. By looking at the data, you’ll be able to see what changes you might need to do next time, or if there are questions that require further research.

6. Verify your findings

Your first attempt gives you the baseline figures to compare the new results to. You can then run another experiment to verify your findings.

7. Do follow-up or supplemental research

You can supplement your original findings by carrying out research that goes deeper into causes or explores the topic in more detail. One of the best ways to do this is to use a survey. See ‘Use surveys to help your experiment’.

Identifying causal relationships between variables

To verify if a causal relationship exists, you have to satisfy the following criteria:

• Nonspurious association

A clear correlation exists between one cause and the effect. In other words, no ‘third’ that relates to both (cause and effect) should exist.

• Temporal sequence

The cause occurs before the effect. For example, increased ad spend on product marketing would contribute to higher product sales.

• Concomitant variation

The variation between the two variables is systematic. For example, if a company doesn’t change its IT policies and technology stack, then changes in employee productivity were not caused by IT policies or technology.

How surveys help your causal research experiments?

There are some surveys that are perfect for assisting researchers with understanding cause and effect. These include:

• Employee Satisfaction Survey – An introductory employee satisfaction survey that provides you with an overview of your current employee experience.
• Manager Feedback Survey – An introductory manager feedback survey geared toward improving your skills as a leader with valuable feedback from your team.
• Net Promoter Score (NPS) Survey – Measure customer loyalty and understand how your customers feel about your product or service using one of the world’s best-recognized metrics.
• Employee Engagement Survey – An entry-level employee engagement survey that provides you with an overview of your current employee experience.
• Customer Satisfaction Survey – Evaluate how satisfied your customers are with your company, including the products and services you provide and how they are treated when they buy from you.
• Employee Exit Interview Survey – Understand why your employees are leaving and how they’ll speak about your company once they’re gone.
• Product Research Survey – Evaluate your consumers’ reaction to a new product or product feature across every stage of the product development journey.
• Brand Awareness Survey – Track the level of brand awareness in your target market, including current and potential future customers.
• Online Purchase Feedback Survey – Find out how well your online shopping experience performs against customer needs and expectations.

That covers the fundamentals of causal research and should give you a foundation for ongoing studies to assess opportunities, problems, and risks across your market, product, customer, and employee segments.

If you want to transform your research, empower your teams and get insights on tap to get ahead of the competition, maybe it’s time to leverage Qualtrics CoreXM.

Qualtrics CoreXM provides a single platform for data collection and analysis across every part of your business — from customer feedback to product concept testing. What’s more, you can integrate it with your existing tools and services thanks to a flexible API.

Qualtrics CoreXM offers you as much or as little power and complexity as you need, so whether you’re running simple surveys or more advanced forms of research, it can deliver every time.

Related resources

Market intelligence 10 min read, marketing insights 11 min read, ethnographic research 11 min read, qualitative vs quantitative research 13 min read, qualitative research questions 11 min read, qualitative research design 12 min read, primary vs secondary research 14 min read, request demo.

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What is causal research design?

Last updated

14 May 2023

Reviewed by

Examining these relationships gives researchers valuable insights into the mechanisms that drive the phenomena they are investigating.

Organizations primarily use causal research design to identify, determine, and explore the impact of changes within an organization and the market. You can use a causal research design to evaluate the effects of certain changes on existing procedures, norms, and more.

This article explores causal research design, including its elements, advantages, and disadvantages.

Analyze your causal research

Dovetail streamlines causal research analysis to help you uncover and share actionable insights

• Components of causal research

You can demonstrate the existence of cause-and-effect relationships between two factors or variables using specific causal information, allowing you to produce more meaningful results and research implications.

These are the key inputs for causal research:

The timeline of events

Ideally, the cause must occur before the effect. You should review the timeline of two or more separate events to determine the independent variables (cause) from the dependent variables (effect) before developing a hypothesis. 

If the cause occurs before the effect, you can link cause and effect and develop a hypothesis .

For instance, an organization may notice a sales increase. Determining the cause would help them reproduce these results. 

Upon review, the business realizes that the sales boost occurred right after an advertising campaign. The business can leverage this time-based data to determine whether the advertising campaign is the independent variable that caused a change in sales. 

Evaluation of confounding variables

In most cases, you need to pinpoint the variables that comprise a cause-and-effect relationship when using a causal research design. This uncovers a more accurate conclusion. 

Co-variations between a cause and effect must be accurate, and a third factor shouldn’t relate to cause and effect. 

Observing changes

Variation links between two variables must be clear. A quantitative change in effect must happen solely due to a quantitative change in the cause. 

You can test whether the independent variable changes the dependent variable to evaluate the validity of a cause-and-effect relationship. A steady change between the two variables must occur to back up your hypothesis of a genuine causal effect. 

• Why is causal research useful?

Causal research allows market researchers to predict hypothetical occurrences and outcomes while enhancing existing strategies. Organizations can use this concept to develop beneficial plans. 

Causal research is also useful as market researchers can immediately deduce the effect of the variables on each other under real-world conditions. 

Once researchers complete their first experiment, they can use their findings. Applying them to alternative scenarios or repeating the experiment to confirm its validity can produce further insights. 

Businesses widely use causal research to identify and comprehend the effect of strategic changes on their profits. 

• How does causal research compare and differ from other research types?

Other research types that identify relationships between variables include exploratory and descriptive research . 

Here’s how they compare and differ from causal research designs:

Exploratory research

An exploratory research design evaluates situations where a problem or opportunity's boundaries are unclear. You can use this research type to test various hypotheses and assumptions to establish facts and understand a situation more clearly.

You can also use exploratory research design to navigate a topic and discover the relevant variables. This research type allows flexibility and adaptability as the experiment progresses, particularly since no area is off-limits.

It’s worth noting that exploratory research is unstructured and typically involves collecting qualitative data . This provides the freedom to tweak and amend the research approach according to your ongoing thoughts and assessments. 

Unfortunately, this exposes the findings to the risk of bias and may limit the extent to which a researcher can explore a topic. 

This table compares the key characteristics of causal and exploratory research:

Descriptive research

This research design involves capturing and describing the traits of a population, situation, or phenomenon. Descriptive research focuses more on the " what " of the research subject and less on the " why ."

Since descriptive research typically happens in a real-world setting, variables can cross-contaminate others. This increases the challenge of isolating cause-and-effect relationships. 

You may require further research if you need more causal links. 

This table compares the key characteristics of causal and descriptive research.  

Causal research examines a research question’s variables and how they interact. It’s easier to pinpoint cause and effect since the experiment often happens in a controlled setting. 

Researchers can conduct causal research at any stage, but they typically use it once they know more about the topic.

In contrast, causal research tends to be more structured and can be combined with exploratory and descriptive research to help you attain your research goals. 

• How can you use causal research effectively?

Here are common ways that market researchers leverage causal research effectively:

Market and advertising research

Do you want to know if your new marketing campaign is affecting your organization positively? You can use causal research to determine the variables causing negative or positive impacts on your campaign. 

Improving customer experiences and loyalty levels

Consumers generally enjoy purchasing from brands aligned with their values. They’re more likely to purchase from such brands and positively represent them to others. 

You can use causal research to identify the variables contributing to increased or reduced customer acquisition and retention rates. 

Could the cause of increased customer retention rates be streamlined checkout? 

Perhaps you introduced a new solution geared towards directly solving their immediate problem. 

Whatever the reason, causal research can help you identify the cause-and-effect relationship. You can use this to enhance your customer experiences and loyalty levels.

Improving problematic employee turnover rates

Is your organization experiencing skyrocketing attrition rates? 

You can leverage the features and benefits of causal research to narrow down the possible explanations or variables with significant effects on employees quitting. 

This way, you can prioritize interventions, focusing on the highest priority causal influences, and begin to tackle high employee turnover rates. 

• Advantages of causal research

The main benefits of causal research include the following:

Effectively test new ideas

If causal research can pinpoint the precise outcome through combinations of different variables, researchers can test ideas in the same manner to form viable proof of concepts.

Achieve more objective results

Market researchers typically use random sampling techniques to choose experiment participants or subjects in causal research. This reduces the possibility of exterior, sample, or demography-based influences, generating more objective results. 

Improved business processes

Causal research helps businesses understand which variables positively impact target variables, such as customer loyalty or sales revenues. This helps them improve their processes, ROI, and customer and employee experiences.

Guarantee reliable and accurate results

Upon identifying the correct variables, researchers can replicate cause and effect effortlessly. This creates reliable data and results to draw insights from. 

Internal organization improvements

Businesses that conduct causal research can make informed decisions about improving their internal operations and enhancing employee experiences. 

• Disadvantages of causal research

Like any other research method, casual research has its set of drawbacks that include:

Extra research to ensure validity

Researchers can't simply rely on the outcomes of causal research since it isn't always accurate. There may be a need to conduct other research types alongside it to ensure accurate output.

Coincidence

Coincidence tends to be the most significant error in causal research. Researchers often misinterpret a coincidental link between a cause and effect as a direct causal link. 

Administration challenges

Causal research can be challenging to administer since it's impossible to control the impact of extraneous variables . 

Giving away your competitive advantage

If you intend to publish your research, it exposes your information to the competition. 

Competitors may use your research outcomes to identify your plans and strategies to enter the market before you. 

• Causal research examples

Multiple fields can use causal research, so it serves different purposes, such as. 

Customer loyalty research

Organizations and employees can use causal research to determine the best customer attraction and retention approaches. 

They monitor interactions between customers and employees to identify cause-and-effect patterns. That could be a product demonstration technique resulting in higher or lower sales from the same customers. 

Example: Business X introduces a new individual marketing strategy for a small customer group and notices a measurable increase in monthly subscriptions. 

Upon getting identical results from different groups, the business concludes that the individual marketing strategy resulted in the intended causal relationship.

Advertising research

Businesses can also use causal research to implement and assess advertising campaigns. 

Example: Business X notices a 7% increase in sales revenue a few months after a business introduces a new advertisement in a certain region. The business can run the same ad in random regions to compare sales data over the same period. 

This will help the company determine whether the ad caused the sales increase. If sales increase in these randomly selected regions, the business could conclude that advertising campaigns and sales share a cause-and-effect relationship. 

Educational research

Academics, teachers, and learners can use causal research to explore the impact of politics on learners and pinpoint learner behavior trends. 

Example: College X notices that more IT students drop out of their program in their second year, which is 8% higher than any other year. 

The college administration can interview a random group of IT students to identify factors leading to this situation, including personal factors and influences. 

With the help of in-depth statistical analysis, the institution's researchers can uncover the main factors causing dropout. They can create immediate solutions to address the problem.

Is a causal variable dependent or independent?

When two variables have a cause-and-effect relationship, the cause is often called the independent variable. As such, the effect variable is dependent, i.e., it depends on the independent causal variable. An independent variable is only causal under experimental conditions. 

What are the three criteria for causality?

The three conditions for causality are:

Temporality/temporal precedence: The cause must precede the effect.

Rationality: One event predicts the other with an explanation, and the effect must vary in proportion to changes in the cause.

Control for extraneous variables: The covariables must not result from other variables.  

Is causal research experimental?

Causal research is mostly explanatory. Causal studies focus on analyzing a situation to explore and explain the patterns of relationships between variables. 

Further, experiments are the primary data collection methods in studies with causal research design. However, as a research design, causal research isn't entirely experimental.

What is the difference between experimental and causal research design?

One of the main differences between causal and experimental research is that in causal research, the research subjects are already in groups since the event has already happened. 

On the other hand, researchers randomly choose subjects in experimental research before manipulating the variables.

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The Craft of Writing a Strong Hypothesis

Table of Contents

Writing a hypothesis is one of the essential elements of a scientific research paper. It needs to be to the point, clearly communicating what your research is trying to accomplish. A blurry, drawn-out, or complexly-structured hypothesis can confuse your readers. Or worse, the editor and peer reviewers.

A captivating hypothesis is not too intricate. This blog will take you through the process so that, by the end of it, you have a better idea of how to convey your research paper's intent in just one sentence.

What is a Hypothesis?

The first step in your scientific endeavor, a hypothesis, is a strong, concise statement that forms the basis of your research. It is not the same as a thesis statement , which is a brief summary of your research paper .

The sole purpose of a hypothesis is to predict your paper's findings, data, and conclusion. It comes from a place of curiosity and intuition . When you write a hypothesis, you're essentially making an educated guess based on scientific prejudices and evidence, which is further proven or disproven through the scientific method.

The reason for undertaking research is to observe a specific phenomenon. A hypothesis, therefore, lays out what the said phenomenon is. And it does so through two variables, an independent and dependent variable.

The independent variable is the cause behind the observation, while the dependent variable is the effect of the cause. A good example of this is “mixing red and blue forms purple.” In this hypothesis, mixing red and blue is the independent variable as you're combining the two colors at your own will. The formation of purple is the dependent variable as, in this case, it is conditional to the independent variable.

Different Types of Hypotheses‌

Types of hypotheses

Some would stand by the notion that there are only two types of hypotheses: a Null hypothesis and an Alternative hypothesis. While that may have some truth to it, it would be better to fully distinguish the most common forms as these terms come up so often, which might leave you out of context.

Apart from Null and Alternative, there are Complex, Simple, Directional, Non-Directional, Statistical, and Associative and casual hypotheses. They don't necessarily have to be exclusive, as one hypothesis can tick many boxes, but knowing the distinctions between them will make it easier for you to construct your own.

1. Null hypothesis

A null hypothesis proposes no relationship between two variables. Denoted by H 0 , it is a negative statement like “Attending physiotherapy sessions does not affect athletes' on-field performance.” Here, the author claims physiotherapy sessions have no effect on on-field performances. Even if there is, it's only a coincidence.

2. Alternative hypothesis

Considered to be the opposite of a null hypothesis, an alternative hypothesis is donated as H1 or Ha. It explicitly states that the dependent variable affects the independent variable. A good  alternative hypothesis example is “Attending physiotherapy sessions improves athletes' on-field performance.” or “Water evaporates at 100 °C. ” The alternative hypothesis further branches into directional and non-directional.

• Directional hypothesis: A hypothesis that states the result would be either positive or negative is called directional hypothesis. It accompanies H1 with either the ‘<' or ‘>' sign.
• Non-directional hypothesis: A non-directional hypothesis only claims an effect on the dependent variable. It does not clarify whether the result would be positive or negative. The sign for a non-directional hypothesis is ‘≠.'

3. Simple hypothesis

A simple hypothesis is a statement made to reflect the relation between exactly two variables. One independent and one dependent. Consider the example, “Smoking is a prominent cause of lung cancer." The dependent variable, lung cancer, is dependent on the independent variable, smoking.

4. Complex hypothesis

In contrast to a simple hypothesis, a complex hypothesis implies the relationship between multiple independent and dependent variables. For instance, “Individuals who eat more fruits tend to have higher immunity, lesser cholesterol, and high metabolism.” The independent variable is eating more fruits, while the dependent variables are higher immunity, lesser cholesterol, and high metabolism.

5. Associative and casual hypothesis

Associative and casual hypotheses don't exhibit how many variables there will be. They define the relationship between the variables. In an associative hypothesis, changing any one variable, dependent or independent, affects others. In a casual hypothesis, the independent variable directly affects the dependent.

6. Empirical hypothesis

Also referred to as the working hypothesis, an empirical hypothesis claims a theory's validation via experiments and observation. This way, the statement appears justifiable and different from a wild guess.

Say, the hypothesis is “Women who take iron tablets face a lesser risk of anemia than those who take vitamin B12.” This is an example of an empirical hypothesis where the researcher  the statement after assessing a group of women who take iron tablets and charting the findings.

7. Statistical hypothesis

The point of a statistical hypothesis is to test an already existing hypothesis by studying a population sample. Hypothesis like “44% of the Indian population belong in the age group of 22-27.” leverage evidence to prove or disprove a particular statement.

Characteristics of a Good Hypothesis

Writing a hypothesis is essential as it can make or break your research for you. That includes your chances of getting published in a journal. So when you're designing one, keep an eye out for these pointers:

• A research hypothesis has to be simple yet clear to look justifiable enough.
• It has to be testable — your research would be rendered pointless if too far-fetched into reality or limited by technology.
• It has to be precise about the results —what you are trying to do and achieve through it should come out in your hypothesis.
• A research hypothesis should be self-explanatory, leaving no doubt in the reader's mind.
• If you are developing a relational hypothesis, you need to include the variables and establish an appropriate relationship among them.
• A hypothesis must keep and reflect the scope for further investigations and experiments.

Separating a Hypothesis from a Prediction

Outside of academia, hypothesis and prediction are often used interchangeably. In research writing, this is not only confusing but also incorrect. And although a hypothesis and prediction are guesses at their core, there are many differences between them.

A hypothesis is an educated guess or even a testable prediction validated through research. It aims to analyze the gathered evidence and facts to define a relationship between variables and put forth a logical explanation behind the nature of events.

Predictions are assumptions or expected outcomes made without any backing evidence. They are more fictionally inclined regardless of where they originate from.

For this reason, a hypothesis holds much more weight than a prediction. It sticks to the scientific method rather than pure guesswork. "Planets revolve around the Sun." is an example of a hypothesis as it is previous knowledge and observed trends. Additionally, we can test it through the scientific method.

Whereas "COVID-19 will be eradicated by 2030." is a prediction. Even though it results from past trends, we can't prove or disprove it. So, the only way this gets validated is to wait and watch if COVID-19 cases end by 2030.

Finally, How to Write a Hypothesis

Quick tips on writing a hypothesis

1.  Be clear about your research question

A hypothesis should instantly address the research question or the problem statement. To do so, you need to ask a question. Understand the constraints of your undertaken research topic and then formulate a simple and topic-centric problem. Only after that can you develop a hypothesis and further test for evidence.

2. Carry out a recce

Once you have your research's foundation laid out, it would be best to conduct preliminary research. Go through previous theories, academic papers, data, and experiments before you start curating your research hypothesis. It will give you an idea of your hypothesis's viability or originality.

Making use of references from relevant research papers helps draft a good research hypothesis. SciSpace Discover offers a repository of over 270 million research papers to browse through and gain a deeper understanding of related studies on a particular topic. Additionally, you can use SciSpace Copilot , your AI research assistant, for reading any lengthy research paper and getting a more summarized context of it. A hypothesis can be formed after evaluating many such summarized research papers. Copilot also offers explanations for theories and equations, explains paper in simplified version, allows you to highlight any text in the paper or clip math equations and tables and provides a deeper, clear understanding of what is being said. This can improve the hypothesis by helping you identify potential research gaps.

3. Create a 3-dimensional hypothesis

Variables are an essential part of any reasonable hypothesis. So, identify your independent and dependent variable(s) and form a correlation between them. The ideal way to do this is to write the hypothetical assumption in the ‘if-then' form. If you use this form, make sure that you state the predefined relationship between the variables.

In another way, you can choose to present your hypothesis as a comparison between two variables. Here, you must specify the difference you expect to observe in the results.

4. Write the first draft

Now that everything is in place, it's time to write your hypothesis. For starters, create the first draft. In this version, write what you expect to find from your research.

Clearly separate your independent and dependent variables and the link between them. Don't fixate on syntax at this stage. The goal is to ensure your hypothesis addresses the issue.

5. Proof your hypothesis

After preparing the first draft of your hypothesis, you need to inspect it thoroughly. It should tick all the boxes, like being concise, straightforward, relevant, and accurate. Your final hypothesis has to be well-structured as well.

Research projects are an exciting and crucial part of being a scholar. And once you have your research question, you need a great hypothesis to begin conducting research. Thus, knowing how to write a hypothesis is very important.

Now that you have a firmer grasp on what a good hypothesis constitutes, the different kinds there are, and what process to follow, you will find it much easier to write your hypothesis, which ultimately helps your research.

Now it's easier than ever to streamline your research workflow with SciSpace Discover . Its integrated, comprehensive end-to-end platform for research allows scholars to easily discover, write and publish their research and fosters collaboration.

It includes everything you need, including a repository of over 270 million research papers across disciplines, SEO-optimized summaries and public profiles to show your expertise and experience.

If you found these tips on writing a research hypothesis useful, head over to our blog on Statistical Hypothesis Testing to learn about the top researchers, papers, and institutions in this domain.

Frequently Asked Questions (FAQs)

1. what is the definition of hypothesis.

According to the Oxford dictionary, a hypothesis is defined as “An idea or explanation of something that is based on a few known facts, but that has not yet been proved to be true or correct”.

2. What is an example of hypothesis?

The hypothesis is a statement that proposes a relationship between two or more variables. An example: "If we increase the number of new users who join our platform by 25%, then we will see an increase in revenue."

3. What is an example of null hypothesis?

A null hypothesis is a statement that there is no relationship between two variables. The null hypothesis is written as H0. The null hypothesis states that there is no effect. For example, if you're studying whether or not a particular type of exercise increases strength, your null hypothesis will be "there is no difference in strength between people who exercise and people who don't."

4. What are the types of research?

• Fundamental research

• Applied research

• Qualitative research

• Quantitative research

• Mixed research

• Exploratory research

• Longitudinal research

• Cross-sectional research

• Field research

• Laboratory research

• Fixed research

• Flexible research

• Action research

• Policy research

• Classification research

• Comparative research

• Causal research

• Inductive research

• Deductive research

5. How to write a hypothesis?

• Your hypothesis should be able to predict the relationship and outcome.

• Avoid wordiness by keeping it simple and brief.

• Your hypothesis should contain observable and testable outcomes.

• Your hypothesis should be relevant to the research question.

6. What are the 2 types of hypothesis?

• Null hypotheses are used to test the claim that "there is no difference between two groups of data".

• Alternative hypotheses test the claim that "there is a difference between two data groups".

7. Difference between research question and research hypothesis?

A research question is a broad, open-ended question you will try to answer through your research. A hypothesis is a statement based on prior research or theory that you expect to be true due to your study. Example - Research question: What are the factors that influence the adoption of the new technology? Research hypothesis: There is a positive relationship between age, education and income level with the adoption of the new technology.

8. What is plural for hypothesis?

The plural of hypothesis is hypotheses. Here's an example of how it would be used in a statement, "Numerous well-considered hypotheses are presented in this part, and they are supported by tables and figures that are well-illustrated."

9. What is the red queen hypothesis?

The red queen hypothesis in evolutionary biology states that species must constantly evolve to avoid extinction because if they don't, they will be outcompeted by other species that are evolving. Leigh Van Valen first proposed it in 1973; since then, it has been tested and substantiated many times.

10. Who is known as the father of null hypothesis?

The father of the null hypothesis is Sir Ronald Fisher. He published a paper in 1925 that introduced the concept of null hypothesis testing, and he was also the first to use the term itself.

11. When to reject null hypothesis?

You need to find a significant difference between your two populations to reject the null hypothesis. You can determine that by running statistical tests such as an independent sample t-test or a dependent sample t-test. You should reject the null hypothesis if the p-value is less than 0.05.

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An Introduction to Causal Inference *

Judea pearl.

* University of California, Los Angeles, ude.alcu.sc@aeduj

This paper summarizes recent advances in causal inference and underscores the paradigmatic shifts that must be undertaken in moving from traditional statistical analysis to causal analysis of multivariate data. Special emphasis is placed on the assumptions that underlie all causal inferences, the languages used in formulating those assumptions, the conditional nature of all causal and counterfactual claims, and the methods that have been developed for the assessment of such claims. These advances are illustrated using a general theory of causation based on the Structural Causal Model (SCM) described in Pearl (2000a) , which subsumes and unifies other approaches to causation, and provides a coherent mathematical foundation for the analysis of causes and counterfactuals. In particular, the paper surveys the development of mathematical tools for inferring (from a combination of data and assumptions) answers to three types of causal queries: those about (1) the effects of potential interventions, (2) probabilities of counterfactuals, and (3) direct and indirect effects (also known as "mediation"). Finally, the paper defines the formal and conceptual relationships between the structural and potential-outcome frameworks and presents tools for a symbiotic analysis that uses the strong features of both. The tools are demonstrated in the analyses of mediation, causes of effects, and probabilities of causation.

1. Introduction

Most studies in the health, social and behavioral sciences aim to answer causal rather than associative – questions. Such questions require some knowledge of the data-generating process, and cannot be computed from the data alone, nor from the distributions that govern the data. Remarkably, although much of the conceptual framework and algorithmic tools needed for tackling such problems are now well established, they are not known to many of the researchers who could put them into practical use. Solving causal problems systematically requires certain extensions in the standard mathematical language of statistics, and these extensions are not typically emphasized in the mainstream literature. As a result, many statistical researchers have not yet benefited from causal inference results in (i) counterfactual analysis, (ii) nonparametric structural equations, (iii) graphical models, and (iv) the symbiosis between counterfactual and graphical methods. This survey aims at making these contemporary advances more accessible by providing a gentle introduction to causal inference for a more in-depth treatment and its methodological principles (see ( Pearl, 2000a , 2009a , b )).

In Section 2, we discuss coping with untested assumptions and new mathematical notation which is required to move from associational to causal statistics. Section 3.1 introduces the fundamentals of the structural theory of causation and uses these modeling fundamentals to represent interventions and develop mathematical tools for estimating causal effects (Section 3.3) and counterfactual quantities (Section 3.4). Section 4 outlines a general methodology to guide problems of causal inference: Define, Assume, Identify and Estimate, with each step benefiting from the tools developed in Section 3.

Section 5 relates these tools to those used in the potential-outcome framework, and offers a formal mapping between the two frameworks and a symbiosis (Section 5.3) that exploits the best features of both. Finally, the benefit of this symbiosis is demonstrated in Section 6, in which the structure-based logic of counterfactuals is harnessed to estimate causal quantities that cannot be defined within the paradigm of controlled randomized experiments. These include direct and indirect effects, the effect of treatment on the treated, and questions of attribution, i.e., whether one event can be deemed “responsible” for another.

2. From Association to Causation

2.1. understanding the distinction and its implications.

The aim of standard statistical analysis is to assess parameters of a distribution from samples drawn of that distribution. With the help of such parameters, associations among variables can be inferred, which permits the researcher to estimate probabilities of past and future events and update those probabilities in light of new information. These tasks are managed well by standard statistical analysis so long as experimental conditions remain the same. Causal analysis goes one step further; its aim is to infer probabilities under conditions that are changing , for example, changes induced by treatments or external interventions.

This distinction implies that causal and associational concepts do not mix; there is nothing in a distribution function to tell us how that distribution would differ if external conditions were to change—say from observational to experimental setup—because the laws of probability theory do not dictate how one property of a distribution ought to change when another property is modified. This information must be provided by causal assumptions which identify relationships that remain invariant when external conditions change.

A useful demarcation line between associational and causal concepts crisp and easy to apply, can be formulated as follows. An associational concept is any relationship that can be defined in terms of a joint distribution of observed variables, and a causal concept is any relationship that cannot be defined from the distribution alone. Examples of associational concepts are: correlation, regression, dependence, conditional independence, likelihood, collapsibility, propensity score, risk ratio, odds ratio, marginalization, conditionalization, “controlling for,” and many more. Examples of causal concepts are: randomization, influence, effect, confounding, “holding constant,” disturbance, error terms, structural coefficients, spurious correlation, faithfulness/stability, instrumental variables, intervention, explanation, and attribution. The former can, while the latter cannot be defined in term of distribution functions.

This demarcation line is extremely useful in tracing the assumptions that are needed for substantiating various types of scientific claims. Every claim invoking causal concepts must rely on some premises that invoke such concepts; it cannot be inferred from, or even defined in terms statistical associations alone.

This distinction further implies that causal relations cannot be expressed in the language of probability and, hence, that any mathematical approach to causal analysis must acquire new notation – probability calculus is insufficient. To illustrate, the syntax of probability calculus does not permit us to express the simple fact that “symptoms do not cause diseases,” let alone draw mathematical conclusions from such facts. All we can say is that two events are dependent—meaning that if we find one, we can expect to encounter the other, but we cannot distinguish statistical dependence, quantified by the conditional probability P ( disease | symptom ) from causal dependence, for which we have no expression in standard probability calculus.

2.2. Untested assumptions and new notation

The preceding two requirements: (1) to commence causal analysis with untested, 1 theoretically or judgmentally based assumptions, and (2) to extend the syntax of probability calculus, constitute the two primary barriers to the acceptance of causal analysis among professionals with traditional training in statistics.

Associational assumptions, even untested, are testable in principle, given sufficiently large sample and sufficiently fine measurements. Causal assumptions, in contrast, cannot be verified even in principle, unless one resorts to experimental control. This difference stands out in Bayesian analysis. Though the priors that Bayesians commonly assign to statistical parameters are untested quantities, the sensitivity to these priors tends to diminish with increasing sample size. In contrast, sensitivity to prior causal assumptions, say that treatment does not change gender, remains substantial regardless of sample size.

This makes it doubly important that the notation we use for expressing causal assumptions be cognitively meaningful and unambiguous so that one can clearly judge the plausibility or inevitability of the assumptions articulated. Statisticians can no longer ignore the mental representation in which scientists store experiential knowledge, since it is this representation, and the language used to access it that determine the reliability of the judgments upon which the analysis so crucially depends.

Those versed in the potential-outcome notation ( Neyman, 1923 , Rubin, 1974 , Holland, 1988 ), can recognize causal expressions through the subscripts that are attached to counterfactual events and variables, e.g. Y x ( u ) or Z xy . (Some authors use parenthetical expressions, e.g. Y (0), Y (1), Y ( x , u ) or Z ( x , y ).) The expression Y x ( u ), for example, stands for the value that outcome Y would take in individual u , had treatment X been at level x . If u is chosen at random, Y x is a random variable, and one can talk about the probability that Y x would attain a value y in the population, written P ( Y x = y ) (see Section 5 for semantics). Alternatively, Pearl (1995) used expressions of the form P ( Y = y | set ( X = x )) or P ( Y = y | do ( X = x )) to denote the probability (or frequency) that event ( Y = y ) would occur if treatment condition X = x were enforced uniformly over the population. 2 Still a third notation that distinguishes causal expressions is provided by graphical models, where the arrows convey causal directionality.

However, few have taken seriously the textbook requirement that any introduction of new notation must entail a systematic definition of the syntax and semantics that governs the notation. Moreover, in the bulk of the statistical literature before 2000, causal claims rarely appear in the mathematics. They surface only in the verbal interpretation that investigators occasionally attach to certain associations, and in the verbal description with which investigators justify assumptions. For example, the assumption that a covariate not be affected by a treatment, a necessary assumption for the control of confounding ( Cox, 1958 , p. 48), is expressed in plain English, not in a mathematical expression.

The next section provides a conceptualization that overcomes these mental barriers by offering a friendly mathematical machinery for cause-effect analysis and a formal foundation for counterfactual analysis.

3. Structural Models, Diagrams, Causal Effects, and Counterfactuals

Any conception of causation worthy of the title “theory” must be able to (1) represent causal questions in some mathematical language, (2) provide a precise language for communicating assumptions under which the questions need to be answered, (3) provide a systematic way of answering at least some of these questions and labeling others “unanswerable,” and (4) provide a method of determining what assumptions or new measurements would be needed to answer the “unanswerable” questions.

A “general theory” should do more. In addition to embracing all questions judged to have causal character, a general theory must also subsume any other theory or method that scientists have found useful in exploring the various aspects of causation. In other words, any alternative theory needs to evolve as a special case of the “general theory” when restrictions are imposed on either the model, the type of assumptions admitted, or the language in which those assumptions are cast.

The structural theory that we use in this survey satisfies the criteria above. It is based on the Structural Causal Model (SCM) developed in ( Pearl, 1995 , 2000a ) which combines features of the structural equation models (SEM) used in economics and social science ( Goldberger, 1973 , Duncan, 1975 ), the potential-outcome framework of Neyman (1923) and Rubin (1974) , and the graphical models developed for probabilistic reasoning and causal analysis ( Pearl, 1988 , Lauritzen, 1996 , Spirtes, Glymour, and Scheines, 2000 , Pearl, 2000a ).

Although the basic elements of SCM were introduced in the mid 1990’s ( Pearl, 1995 ), and have been adapted widely by epidemiologists ( Greenland, Pearl, and Robins, 1999 , Glymour and Greenland, 2008 ), statisticians ( Cox and Wermuth, 2004 , Lauritzen, 2001 ), and social scientists ( Morgan and Winship, 2007 ), its potentials as a comprehensive theory of causation are yet to be fully utilized. Its ramifications thus far include:

• The unification of the graphical, potential outcome, structural equations, decision analytical ( Dawid, 2002 ), interventional ( Woodward, 2003 ), sufficient component ( Rothman, 1976 ) and probabilistic ( Suppes, 1970 ) approaches to causation; with each approach viewed as a restricted version of the SCM.
• The definition, axiomatization and algorithmization of counterfactuals and joint probabilities of counterfactuals
• Reducing the evaluation of “effects of causes,” “mediated effects,” and “causes of effects” to an algorithmic level of analysis.
• Solidifying the mathematical foundations of the potential-outcome model, and formulating the counterfactual foundations of structural equation models.
• Demystifying enigmatic notions such as “confounding,” “mediation,” “ignorability,” “comparability,” “exchangeability (of populations),” “superexogeneity” and others within a single and familiar conceptual framework.
• Weeding out myths and misconceptions from outdated traditions ( Meek and Glymour, 1994 , Greenland et al., 1999 , Cole and Hernán, 2002 , Arah, 2008 , Shrier, 2009 , Pearl, 2009c ).

This section provides a gentle introduction to the structural framework and uses it to present the main advances in causal inference that have emerged in the past two decades.

3.1. A brief introduction to structural equation models

How can one express mathematically the common understanding that symptoms do not cause diseases? The earliest attempt to formulate such relationship mathematically was made in the 1920’s by the geneticist Sewall Wright (1921) . Wright used a combination of equations and graphs to communicate causal relationships. For example, if X stands for a disease variable and Y stands for a certain symptom of the disease, Wright would write a linear equation: 3

where x stands for the level (or severity) of the disease, y stands for the level (or severity) of the symptom, and u Y stands for all factors, other than the disease in question, that could possibly affect Y when X is held constant. In interpreting this equation one should think of a physical process whereby Nature examines the values of x and u and, accordingly, assigns variable Y the value y = βx + u Y . Similarly, to “explain” the occurrence of disease X , one could write x = u X , where U X stands for all factors affecting X .

Equation (1) still does not properly express the causal relationship implied by this assignment process, because algebraic equations are symmetrical objects; if we re-write (1) as

it might be misinterpreted to mean that the symptom influences the disease. To express the directionality of the underlying process, Wright augmented the equation with a diagram, later called “path diagram,” in which arrows are drawn from (perceived) causes to their (perceived) effects, and more importantly, the absence of an arrow makes the empirical claim that Nature assigns values to one variable irrespective of another. In Fig. 1 , for example, the absence of arrow from Y to X represents the claim that symptom Y is not among the factors U X which affect disease X . Thus, in our example, the complete model of a symptom and a disease would be written as in Fig. 1 : The diagram encodes the possible existence of (direct) causal influence of X on Y , and the absence of causal influence of Y on X , while the equations encode the quantitative relationships among the variables involved, to be determined from the data. The parameter β in the equation is called a “path coefficient” and it quantifies the (direct) causal effect of X on Y ; given the numerical values of β and U Y , the equation claims that, a unit increase for X would result in β units increase of Y regardless of the values taken by other variables in the model, and regardless of whether the increase in X originates from external or internal influences.

A simple structural equation model, and its associated diagrams. Unobserved exogenous variables are connected by dashed arrows.

The variables U X and U Y are called “exogenous;” they represent observed or unobserved background factors that the modeler decides to keep unexplained, that is, factors that influence but are not influenced by the other variables (called “endogenous”) in the model. Unobserved exogenous variables are sometimes called “disturbances” or “errors”, they represent factors omitted from the model but judged to be relevant for explaining the behavior of variables in the model. Variable U X , for example, represents factors that contribute to the disease X , which may or may not be correlated with U Y (the factors that influence the symptom Y ). Thus, background factors in structural equations differ fundamentally from residual terms in regression equations. The latters are artifacts of analysis which, by definition, are uncorrelated with the regressors. The formers are part of physical reality (e.g., genetic factors, socio-economic conditions) which are responsible for variations observed in the data; they are treated as any other variable, though we often cannot measure their values precisely and must resign to merely acknowledging their existence and assessing qualitatively how they relate to other variables in the system.

If correlation is presumed possible, it is customary to connect the two variables, U Y and U X , by a dashed double arrow, as shown in Fig. 1(b) .

In reading path diagrams, it is common to use kinship relations such as parent, child, ancestor, and descendent, the interpretation of which is usually self evident. For example, an arrow X → Y designates X as a parent of Y and Y as a child of X . A “path” is any consecutive sequence of edges, solid or dashed. For example, there are two paths between X and Y in Fig. 1(b) , one consisting of the direct arrow X → Y while the other tracing the nodes X , U X , U Y and Y .

Wright’s major contribution to causal analysis, aside from introducing the language of path diagrams, has been the development of graphical rules for writing down the covariance of any pair of observed variables in terms of path coefficients and of covariances among the error terms. In our simple example, one can immediately write the relations

for Fig. 1(a) , and

for Fig. 1(b) (These can be derived of course from the equations, but, for large models, algebraic methods tend to obscure the origin of the derived quantities). Under certain conditions, (e.g. if Cov ( U Y , U X ) = 0), such relationships may allow one to solve for the path coefficients in term of observed covariance terms only, and this amounts to inferring the magnitude of (direct) causal effects from observed, nonexperimental associations, assuming of course that one is prepared to defend the causal assumptions encoded in the diagram.

It is important to note that, in path diagrams, causal assumptions are encoded not in the links but, rather, in the missing links. An arrow merely indicates the possibility of causal connection, the strength of which remains to be determined (from data); a missing arrow represents a claim of zero influence, while a missing double arrow represents a claim of zero covariance. In Fig. 1(a) , for example, the assumptions that permits us to identify the direct effect β are encoded by the missing double arrow between U X and U Y , indicating Cov ( U Y , U X )=0, together with the missing arrow from Y to X . Had any of these two links been added to the diagram, we would not have been able to identify the direct effect β . Such additions would amount to relaxing the assumption Cov ( U Y , U X ) = 0, or the assumption that Y does not effect X , respectively. Note also that both assumptions are causal, not associational, since none can be determined from the joint density of the observed variables, X and Y ; the association between the unobserved terms, U Y and U X , can only be uncovered in an experimental setting; or (in more intricate models, as in Fig. 5 ) from other causal assumptions.

Causal diagram representing the assignment ( Z ), treatment ( X ), and outcome ( Y ) in a clinical trial with imperfect compliance.

Although each causal assumption in isolation cannot be tested, the sum total of all causal assumptions in a model often has testable implications. The chain model of Fig. 2(a) , for example, encodes seven causal assumptions, each corresponding to a missing arrow or a missing double-arrow between a pair of variables. None of those assumptions is testable in isolation, yet the totality of all those assumptions implies that Z is unassociated with Y in every stratum of X . Such testable implications can be read off the diagrams using a graphical criterion known as d-separation ( Pearl, 1988 ).

(a) The diagram associated with the structural model of Eq. (5) . (b) The diagram associated with the modified model of Eq. (6) , representing the intervention do ( X = x 0 ).

Definition 1 ( d -separation) A set S of nodes is said to block a path p if either (i) p contains at least one arrow-emitting node that is in S, or (ii) p contains at least one collision node that is outside S and has no descendant in S. If S blocks all paths from X to Y, it is said to “d-separate X and Y,” and then, X and Y are independent given S, written X ⊥⊥ Y|S .

To illustrate, the path U Z → Z → X → Y is blocked by S = { Z } and by S = { X }, since each emits an arrow along that path. Consequently we can infer that the conditional independencies U Z ⊥⊥ Y | Z and U Z ⊥⊥ Y | X will be satisfied in any probability function that this model can generate, regardless of how we parametrize the arrows. Likewise, the path U Z → Z → X ← U X is blocked by the null set {∅︀} but is not blocked by S = { Y }, since Y is a descendant of the collision node X . Consequently, the marginal independence U Z ⊥⊥ U X will hold in the distribution, but U Z ⊥⊥ U X | Y may or may not hold. This special handling of collision nodes (or colliders, e.g., Z → X ← U X ) reflects a general phenomenon known as Berkson’s paradox ( Berkson, 1946 ), whereby observations on a common consequence of two independent causes render those causes dependent. For example, the outcomes of two independent coins are rendered dependent by the testimony that at least one of them is a tail.

The conditional independencies entailed by d -separation constitute the main opening through which the assumptions embodied in structural equation models can confront the scrutiny of nonexperimental data. In other words, almost all statistical tests capable of invalidating the model are entailed by those implications. 4

3.2. From linear to nonparametric models and graphs

Structural equation modeling (SEM) has been the main vehicle for effect analysis in economics and the behavioral and social sciences ( Goldberger, 1972 , Duncan, 1975 , Bollen, 1989 ). However, the bulk of SEM methodology was developed for linear analysis and, until recently, no comparable methodology has been devised to extend its capabilities to models involving dichotomous variables or nonlinear dependencies. A central requirement for any such extension is to detach the notion of “effect” from its algebraic representation as a coefficient in an equation, and redefine “effect” as a general capacity to transmit changes among variables. Such an extension, based on simulating hypothetical interventions in the model, was proposed in ( Haavelmo, 1943 , Strotz and Wold, 1960 , Spirtes, Glymour, and Scheines, 1993 , Pearl, 1993a , 2000a , Lindley, 2002 ) and has led to new ways of defining and estimating causal effects in nonlinear and nonparametric models (that is, models in which the functional form of the equations is unknown).

The central idea is to exploit the invariant characteristics of structural equations without committing to a specific functional form. For example, the nonparametric interpretation of the diagram of Fig. 2(a) corresponds to a set of three functions, each corresponding to one of the observed variables:

where in this particular example U Z , U X and U Y are assumed to be jointly independent but, otherwise, arbitrarily distributed. Each of these functions represents a causal process (or mechanism) that determines the value of the left variable (output) from those on the right variables (inputs). The absence of a variable from the right hand side of an equation encodes the assumption that Nature ignores that variable in the process of determining the value of the output variable. For example, the absence of variable Z from the arguments of f Y conveys the empirical claim that variations in Z will leave Y unchanged, as long as variables U Y , and X remain constant. A system of such functions are said to be structural if they are assumed to be autonomous, that is, each function is invariant to possible changes in the form of the other functions ( Simon, 1953 , Koopmans, 1953 ).

3.2.1. Representing interventions

This feature of invariance permits us to use structural equations as a basis for modeling causal effects and counterfactuals. This is done through a mathematical operator called do ( x ) which simulates physical interventions by deleting certain functions from the model, replacing them by a constant X = x , while keeping the rest of the model unchanged. For example, to emulate an intervention do ( x 0 ) that holds X constant (at X = x 0 ) in model M of Fig. 2(a) , we replace the equation for x in Eq. (5) with x = x 0 , and obtain a new model, M x 0 ,

the graphical description of which is shown in Fig. 2(b) .

The joint distribution associated with the modified model, denoted P ( z , y | do ( x 0 )) describes the post-intervention distribution of variables Y and Z (also called “controlled” or “experimental” distribution), to be distinguished from the pre-intervention distribution, P ( x , y , z ), associated with the original model of Eq. (5) . For example, if X represents a treatment variable, Y a response variable, and Z some covariate that affects the amount of treatment received, then the distribution P ( z , y | do ( x 0 )) gives the proportion of individuals that would attain response level Y = y and covariate level Z = z under the hypothetical situation in which treatment X = x 0 is administered uniformly to the population.

In general, we can formally define the post-intervention distribution by the equation:

In words: In the framework of model M , the post-intervention distribution of outcome Y is defined as the probability that model M x assigns to each outcome level Y = y .

From this distribution, one is able to assess treatment efficacy by comparing aspects of this distribution at different levels of x 0 . A common measure of treatment efficacy is the average difference

where x ′ 0 and x 0 are two levels (or types) of treatment selected for comparison. Another measure is the experimental Risk Ratio

The variance Var ( Y | do ( x 0 )), or any other distributional parameter, may also enter the comparison; all these measures can be obtained from the controlled distribution function P ( Y = y | do ( x )) = ∑ z P ( z , y | do ( x )) which was called “causal effect” in Pearl (2000a , 1995) (see footnote 2 ). The central question in the analysis of causal effects is the question of identification : Can the controlled (post-intervention) distribution, P ( Y = y | do ( x )), be estimated from data governed by the pre-intervention distribution, P ( z , x , y )?

The problem of identification has received considerable attention in econometrics ( Hurwicz, 1950 , Marschak, 1950 , Koopmans, 1953 ) and social science ( Duncan, 1975 , Bollen, 1989 ), usually in linear parametric settings, where it reduces to asking whether some model parameter, β , has a unique solution in terms of the parameters of P (the distribution of the observed variables). In the nonparametric formulation, identification is more involved, since the notion of “has a unique solution” does not directly apply to causal quantities such as Q ( M ) = P ( y | do ( x )) which have no distinct parametric signature, and are defined procedurally by simulating an intervention in a causal model M (as in (6)). The following definition overcomes these difficulties:

Definition 2 (Identifiability ( Pearl, 2000a , p. 77)) A quantity Q(M) is identifiable, given a set of assumptions A, if for any two models M 1 and M 2 that satisfy A, we have

In words, the details of M 1 and M 2 do not matter; what matters is that the assumptions in A (e.g., those encoded in the diagram) would constrain the variability of those details in such a way that equality of P ’s would entail equality of Q ’s. When this happens, Q depends on P only, and should therefore be expressible in terms of the parameters of P . The next subsections exemplify and operationalize this notion.

3.2.2. Estimating the effect of interventions

To understand how hypothetical quantities such as P ( y | do ( x )) or E ( Y | do ( x 0 )) can be estimated from actual data and a partially specified model let us begin with a simple demonstration on the model of Fig. 2(a) . We will see that, despite our ignorance of f X , f Y , f Z and P ( u ), E ( Y | do ( x 0 )) is nevertheless identifiable and is given by the conditional expectation E ( Y | X = x 0 ). We do this by deriving and comparing the expressions for these two quantities, as defined by (5) and (6), respectively. The mutilated model in Eq. (6) dictates:

whereas the pre-intervention model of Eq. (5) gives

which is identical to (11). Therefore,

Using a similar derivation, though somewhat more involved, we can show that P ( y | do ( x )) is identifiable and given by the conditional probability P ( y | x ).

We see that the derivation of (13) was enabled by two assumptions; first, Y is a function of X and U Y only, and, second, U Y is independent of { U Z , U X }, hence of X . The latter assumption parallels the celebrated “orthogonality” condition in linear models, Cov ( X , U Y ) = 0, which has been used routinely, often thoughtlessly, to justify the estimation of structural coefficients by regression techniques.

Naturally, if we were to apply this derivation to the linear models of Fig. 1(a) or 1(b) , we would get the expected dependence between Y and the intervention do ( x 0 ):

This equality endows β with its causal meaning as “effect coefficient.” It is extremely important to keep in mind that in structural (as opposed to regressional) models, β is not “interpreted” as an effect coefficient but is “proven” to be one by the derivation above. β will retain this causal interpretation regardless of how X is actually selected (through the function f X , Fig. 2(a) ) and regardless of whether U X and U Y are correlated (as in Fig. 1(b) ) or uncorrelated (as in Fig. 1(a) ). Correlations may only impede our ability to estimate β from nonexperimental data, but will not change its definition as given in (14). Accordingly, and contrary to endless confusions in the literature (see footnote 12 ) structural equations say absolutely nothing about the conditional expectation E ( Y | X = x ). Such connection may exist under special circumstances, e.g., if cov ( X , U Y ) = 0, as in Eq. (13) , but is otherwise irrelevant to the definition or interpretation of β as effect coefficient, or to the empirical claims of Eq. (1) .

The next subsection will circumvent these derivations altogether by reducing the identification problem to a graphical procedure. Indeed, since graphs encode all the information that non-parametric structural equations represent, they should permit us to solve the identification problem without resorting to algebraic analysis.

3.2.3. Causal effects from data and graphs

Causal analysis in graphical models begins with the realization that all causal effects are identifiable whenever the model is Markovian , that is, the graph is acyclic (i.e., containing no directed cycles) and all the error terms are jointly independent. Non-Markovian models, such as those involving correlated errors (resulting from unmeasured confounders), permit identification only under certain conditions, and these conditions too can be determined from the graph structure (Section 3.3). The key to these results rests with the following basic theorem.

Theorem 1 (The Causal Markov Condition) Any distribution generated by a Markovian model M can be factorized as:

where V 1 , V 2 , . . ., V n are the endogenous variables in M, and pa i are (values of) the endogenous “parents” of V i in the causal diagram associated with M.

For example, the distribution associated with the model in Fig. 2(a) can be factorized as

since X is the (endogenous) parent of Y , Z is the parent of X , and Z has no parents.

Corollary 1 (Truncated factorization) For any Markovian model, the distribution generated by an intervention do ( X = x 0 ) on a set X of endogenous variables is given by the truncated factorization

where P(v i | pa i ) are the pre-intervention conditional probabilities. 5

Corollary 1 instructs us to remove from the product of Eq. (15) those factors that quantify how the intervened variables (members of set X ) are influenced by their pre-intervention parents. This removal follows from the fact that the post-intervention model is Markovian as well, hence, following Theorem 1, it must generate a distribution that is factorized according to the modified graph, yielding the truncated product of Corollary 1. In our example of Fig. 2(b) , the distribution P ( z , y | do ( x 0 )) associated with the modified model is given by

where P ( z ) and P ( y | x 0 ) are identical to those associated with the pre-intervention distribution of Eq. (16) . As expected, the distribution of Z is not affected by the intervention, since

while that of Y is sensitive to x 0 , and is given by

This example demonstrates how the (causal) assumptions embedded in the model M permit us to predict the post-intervention distribution from the pre-intervention distribution, which further permits us to estimate the causal effect of X on Y from nonexperimental data, since P ( y | x 0 ) is estimable from such data. Note that we have made no assumption whatsoever on the form of the equations or the distribution of the error terms; it is the structure of the graph alone (specifically, the identity of X ’s parents) that permits the derivation to go through.

The truncated factorization formula enables us to derive causal quantities directly, without dealing with equations or equation modification as in Eqs. (11) – (13) . Consider, for example, the model shown in Fig. 3 , in which the error variables are kept implicit. Instead of writing down the corresponding five nonparametric equations, we can write the joint distribution directly as

where each marginal or conditional probability on the right hand side is directly estimable from the data. Now suppose we intervene and set variable X to x 0 . The post-intervention distribution can readily be written (using the truncated factorization formula (17) ) as

and the causal effect of X on Y can be obtained immediately by marginalizing over the Z variables, giving

Note that this formula corresponds precisely to what is commonly called “adjusting for Z 1 , Z 2 and Z 3 ” and, moreover, we can write down this formula by inspection, without thinking on whether Z 1 , Z 2 and Z 3 are confounders, whether they lie on the causal pathways, and so on. Though such questions can be answered explicitly from the topology of the graph, they are dealt with automatically when we write down the truncated factorization formula and marginalize.

Markovian model illustrating the derivation of the causal effect of X on Y , Eq. (20) . Error terms are not shown explicitly.

Note also that the truncated factorization formula is not restricted to interventions on a single variable; it is applicable to simultaneous or sequential interventions such as those invoked in the analysis of time varying treatment with time varying confounders ( Robins, 1986 , Arjas and Parner, 2004 ). For example, if X and Z 2 are both treatment variables, and Z 1 and Z 3 are measured covariates, then the post-intervention distribution would be

and the causal effect of the treatment sequence do ( X = x ), do ( Z 2 = z 2 ) 6 would be

This expression coincides with Robins’ (1987) G -computation formula, which was derived from a more complicated set of (counterfactual) assumptions. As noted by Robins, the formula dictates an adjustment for covariates (e.g., Z 3 ) that might be affected by previous treatments (e.g., Z 2 ).

3.3. Coping with unmeasured confounders

Things are more complicated when we face unmeasured confounders. For example, it is not immediately clear whether the formula in Eq. (20) can be estimated if any of Z 1 , Z 2 and Z 3 is not measured. A few but challenging algebraic steps would reveal that one can perform the summation over Z 2 to obtain

which means that we need only adjust for Z 1 and Z 3 without ever measuring Z 2 . In general, it can be shown ( Pearl, 2000a , p. 73) that, whenever the graph is Markovian the post-interventional distribution P ( Y = y | do ( X = x )) is given by the following expression:

where T is the set of direct causes of X (also called “parents”) in the graph. This allows us to write (23) directly from the graph, thus skipping the algebra that led to (23). It further implies that, no matter how complicated the model, the parents of X are the only variables that need to be measured to estimate the causal effects of X .

It is not immediately clear however whether other sets of variables beside X ’s parents suffice for estimating the effect of X , whether some algebraic manipulation can further reduce Eq. (23) , or that measurement of Z 3 (unlike Z 1 , or Z 2 ) is necessary in any estimation of P ( y | do ( x 0 )). Such considerations become transparent from a graphical criterion to be discussed next.

3.3.1. Covariate selection – the back-door criterion

Consider an observational study where we wish to find the effect of X on Y , for example, treatment on response, and assume that the factors deemed relevant to the problem are structured as in Fig. 4 ; some are affecting the response, some are affecting the treatment and some are affecting both treatment and response. Some of these factors may be unmeasurable, such as genetic trait or life style, others are measurable, such as gender, age, and salary level. Our problem is to select a subset of these factors for measurement and adjustment, namely, that if we compare treated vs. untreated subjects having the same values of the selected factors, we get the correct treatment effect in that subpopulation of subjects. Such a set of factors is called a “sufficient set” or “admissible set” for adjustment. The problem of defining an admissible set, let alone finding one, has baffled epidemiologists and social scientists for decades (see ( Greenland et al., 1999 , Pearl, 1998 ) for review).

Markovian model illustrating the back-door criterion. Error terms are not shown explicitly.

The following criterion, named “back-door” in ( Pearl, 1993a ), settles this problem by providing a graphical method of selecting admissible sets of factors for adjustment.

Definition 3 (Admissible sets – the back-door criterion) A set S is admissible (or “sufficient”) for adjustment if two conditions hold:

• No element of S is a descendant of X
• The elements of S “block” all “back-door” paths from X to Y, namely all paths that end with an arrow pointing to X.

In this criterion, “blocking” is interpreted as in Definition 1. For example, the set S = { Z 3 } blocks the path X ← W 1 ← Z 1 → Z 3 → Y , because the arrow-emitting node Z 3 is in S . However, the set S = { Z 3 } does not block the path X ← W 1 ← Z 1 → Z 3 ← Z 2 → W 2 → Y , because none of the arrow-emitting nodes, Z 1 and Z 2 , is in S , and the collision node Z 3 is not outside S .

Based on this criterion we see, for example, that the sets { Z 1 , Z 2 , Z 3 }, { Z 1 , Z 3 }, { W 1 , Z 3 }, and { W 2 , Z 3 }, each is sufficient for adjustment, because each blocks all back-door paths between X and Y . The set { Z 3 }, however, is not sufficient for adjustment because, as explained above, it does not block the path X ← W 1 ← Z 1 → Z 3 ← Z 2 → W 2 → Y .

The intuition behind the back-door criterion is as follows. The back-door paths in the diagram carry spurious associations from X to Y , while the paths directed along the arrows from X to Y carry causative associations. Blocking the former paths (by conditioning on S ) ensures that the measured association between X and Y is purely causative, namely, it correctly represents the target quantity: the causal effect of X on Y . The reason for excluding descendants of X (e.g., W 3 or any of its descendants) is given in ( Pearl, 2009b , pp. 338–41).

Formally, the implication of finding an admissible set S is that, stratifying on S is guaranteed to remove all confounding bias relative the causal effect of X on Y . In other words, the risk difference in each stratum of S gives the correct causal effect in that stratum. In the binary case, for example, the risk difference in stratum s of S is given by

while the causal effect (of X on Y ) at that stratum is given by

These two expressions are guaranteed to be equal whenever S is a sufficient set, such as { Z 1 , Z 3 } or { Z 2 , Z 3 } in Fig. 4 . Likewise, the average stratified risk difference, taken over all strata,

gives the correct causal effect of X on Y in the entire population

In general, for multi-valued variables X and Y , finding a sufficient set S permits us to write

Since all factors on the right hand side of the equation are estimable (e.g., by regression) from the pre-interventional data, the causal effect can likewise be estimated from such data without bias.

An equivalent expression for the causal effect (25) can be obtained by multiplying and dividing by the conditional probability P ( X = x | S = s ), giving

from which the name “Inverse Probability Weighting” has evolved ( Pearl, 2000a , pp. 73, 95).

Interestingly, it can be shown that any irreducible sufficient set, S , taken as a unit, satisfies the associational criterion that epidemiologists have been using to define “confounders”. In other words, S must be associated with X and, simultaneously, associated with Y , given X . This need not hold for any specific members of S . For example, the variable Z 3 in Fig. 4 , though it is a member of every sufficient set and hence a confounder, can be unassociated with both Y and X ( Pearl, 2000a , p. 195). Conversely, a pre-treatment variable Z that is associated with both Y and X may need to be excluded from entering a sufficient set.

The back-door criterion allows us to write Eq. (25) directly, by selecting a sufficient set S directly from the diagram, without manipulating the truncated factorization formula. The selection criterion can be applied systematically to diagrams of any size and shape, thus freeing analysts from judging whether “ X is conditionally ignorable given S ,” a formidable mental task required in the potential-response framework ( Rosenbaum and Rubin, 1983 ). The criterion also enables the analyst to search for an optimal set of covariate—namely, a set S that minimizes measurement cost or sampling variability ( Tian, Paz, and Pearl, 1998 ).

All in all, one can safely state that, armed with the back-door criterion, causality has removed “confounding” from its store of enigmatic and controversial concepts.

3.3.2. Confounding equivalence – a graphical test

Another problem that has been given graphical solution recently is that of determining whether adjustment for two sets of covariates would result in the same confounding bias ( Pearl and Paz, 2009 ). The reasons for posing this question are several. First, an investigator may wish to assess, prior to taking any measurement, whether two candidate sets of covariates, differing substantially in dimensionality, measurement error, cost, or sample variability are equally valuable in their bias-reduction potential. Second, assuming that the structure of the underlying DAG is only partially known, one may wish to test, using adjustment, which of two hypothesized structures is compatible with the data. Structures that predict equal response to adjustment for two sets of variables must be rejected if, after adjustment, such equality is not found in the data.

Definition 4 (( c -equivalence)) Define two sets, T and Z of covariates as c-equivalent, (c connotes “confounding”) if the following equality holds:

Definition 5 ((Markov boundary)) For any set of variables S in a DAG G, the Markov boundary S m of S is the minimal subset of S that d-separates X from all other members of S.

In Fig. 4 , for example, the Markov boundary of S = { W 1 , Z 1 , Z 2 , Z 3 } is S m = { W 1 , Z 3 }.

Theorem 2 ( Pearl and Paz, 2009 )

Let Z and T be two sets of variables in G, containing no descendant of X. A necessary and sufficient conditions for Z and T to be c-equivalent is that at least one of the following conditions holds:

• Z m = T m , (i.e., the Markov boundary of Z coincides with that of T)
• Z and T are admissible (i.e., satisfy the back-door condition)

For example, the sets T = { W 1 , Z 3 } and Z = { Z 3 , W 2 } in Fig. 4 are c -equivalent, because each blocks all back-door paths from X to Y . Similarly, the non-admissible sets T = { Z 2 } and Z = { W 2 , Z 2 } are c -equivalent, since their Markov boundaries are the same ( T m = Z m = { Z 2 }). In contrast, the sets { W 1 } and { Z 1 }, although they block the same set of paths in the graph, are not c -equivalent; they fail both conditions of Theorem 2.

Tests for c -equivalence (27) are fairly easy to perform, and they can also be assisted by propensity scores methods. The information that such tests provide can be as powerful as conditional independence tests. The statistical ramification of such tests are explicated in ( Pearl and Paz, 2009 ).

3.3.3. General control of confounding

Adjusting for covariates is only one of many methods that permits us to estimate causal effects in nonexperimental studies. Pearl (1995) has presented examples in which there exists no set of variables that is sufficient for adjustment and where the causal effect can nevertheless be estimated consistently. The estimation, in such cases, employs multi-stage adjustments. For example, if W 3 is the only observed covariate in the model of Fig. 4 , then there exists no sufficient set for adjustment (because no set of observed covariates can block the paths from X to Y through Z 3 ), yet P ( y | do ( x )) can be estimated in two steps; first we estimate P ( w 3 | do ( x )) = P ( w 3 | x ) (by virtue of the fact that there exists no unblocked back-door path from X to W 3 ), second we estimate P ( y | do ( w 3 )) (since X constitutes a sufficient set for the effect of W 3 on Y ) and, finally, we combine the two effects together and obtain

In this example, the variable W 3 acts as a “mediating instrumental variable” ( Pearl, 1993b , Chalak and White, 2006 ).

The analysis used in the derivation and validation of such results invokes mathematical rules of transforming causal quantities, represented by expressions such as P ( Y = y | do ( x )), into do -free expressions derivable from P ( z , x , y ), since only do -free expressions are estimable from non-experimental data. When such a transformation is feasible, we are ensured that the causal quantity is identifiable.

Applications of this calculus to problems involving multiple interventions (e.g., time varying treatments), conditional policies, and surrogate experiments were developed in Pearl and Robins (1995) , Kuroki and Miyakawa (1999) , and Pearl (2000a , Chapters 3–4).

A more recent analysis ( Tian and Pearl, 2002 ) shows that the key to identifiability lies not in blocking paths between X and Y but, rather, in blocking paths between X and its immediate successors on the pathways to Y . All existing criteria for identification are special cases of the one defined in the following theorem:

Theorem 3 ( Tian and Pearl, 2002 ) A sufficient condition for identifying the causal effect P ( y|do ( x )) is that every path between X and any of its children traces at least one arrow emanating from a measured variable. 7

For example, if W 3 is the only observed covariate in the model of Fig. 4 , P ( y | do ( x )) can be estimated since every path from X to W 3 (the only child of X ) traces either the arrow X → W 3 , or the arrow W 3 → Y , both emanating from a measured variable ( W 3 ).

Shpitser and Pearl (2006) have further extended this theorem by (1) presenting a necessary and sufficient condition for identification, and (2) extending the condition from causal effects to any counterfactual expression. The corresponding unbiased estimands for these causal quantities are readable directly from the diagram.

Graph-based methods for effect identification under measurement errors are discussed in ( Pearl, 2009f , Hernán and Cole, 2009 , Cai and Kuroki, 2008 ).

3.3.4. From identification to estimation

The mathematical derivation of causal effect estimands, like Eqs. (25) and (28) is merely a first step toward computing quantitative estimates of those effects from finite samples, using the rich traditions of statistical estimation and machine learning Bayesian as well as non-Bayesian. Although the estimands derived in (25) and (28) are non-parametric, this does not mean that one should refrain from using parametric forms in the estimation phase of the study. Parameterization is in fact necessary when the dimensionality of a problem is high. For example, if the assumptions of Gaussian, zero-mean disturbances and additive interactions are deemed reasonable, then the estimand given in (28) can be converted to the product E ( Y | do ( x )) = r W 3 X r YW 3·X x , where r YZ·X is the (standardized) coefficient of Z in the regression of Y on Z and X . More sophisticated estimation techniques are the “marginal structural models” of ( Robins, 1999 ), and the “propensity score” method of ( Rosenbaum and Rubin, 1983 ) which were found to be particularly useful when dimensionality is high and data are sparse (see Pearl (2009b , pp. 348–52)).

It should be emphasized, however, that contrary to conventional wisdom (e.g., ( Rubin, 2007 , 2009 )), propensity score methods are merely efficient estimators of the right hand side of (25); they entail the same asymptotic bias, and cannot be expected to reduce bias in case the set S does not satisfy the back-door criterion ( Pearl, 2000a , 2009c , d ). Consequently, the prevailing practice of conditioning on as many pre-treatment measurements as possible should be approached with great caution; some covariates (e.g., Z 3 in Fig. 3 ) may actually increase bias if included in the analysis (see footnote 16 ). Using simulation and parametric analysis, Heckman and Navarro-Lozano (2004) and Wooldridge (2009) indeed confirmed the bias-raising potential of certain covariates in propensity-score methods. The graphical tools presented in this section unveil the character of these covariates and show precisely what covariates should, and should not be included in the conditioning set for propensity-score matching (see also ( Pearl and Paz, 2009 , Pearl, 2009e )).

3.4. Counterfactual analysis in structural models

Not all questions of causal character can be encoded in P ( y | do ( x )) type expressions, thus implying that not all causal questions can be answered from experimental studies. For example, questions of attribution (e.g., what fraction of death cases are due to specific exposure?) or of susceptibility (what fraction of the healthy unexposed population would have gotten the disease had they been exposed?) cannot be answered from experimental studies, and naturally, this kind of questions cannot be expressed in P ( y | do ( x )) notation. 8 To answer such questions, a probabilistic analysis of counterfactuals is required, one dedicated to the relation “ Y would be y had X been x in situation U = u ,” denoted Y x ( u ) = y . Remarkably, unknown to most economists and philosophers, structural equation models provide the formal interpretation and symbolic machinery for analyzing such counterfactual relationships. 9

The key idea is to interpret the phrase “had X been x ” as an instruction to make a minimal modification in the current model, which may have assigned X a different value, say X = x ′ , so as to ensure the specified condition X = x . Such a minimal modification amounts to replacing the equation for X by a constant x , as we have done in Eq. (6) . This replacement permits the constant x to differ from the actual value of X (namely f X ( z , u X )) without rendering the system of equations inconsistent, thus yielding a formal interpretation of counterfactuals in multi-stage models, where the dependent variable in one equation may be an independent variable in another.

Definition 6 (Unit-level Counterfactuals – “surgical” definition, Pearl (2000a , p. 98)) Let M be a structural model and M x a modified version of M, with the equation(s) of X replaced by X = x. Denote the solution for Y in the equations of M x by the symbol Y M x (u). The counterfactual Y x (u) (Read: “The value of Y in unit u, had X been x”) is given by:

In words: The counterfactual Y x ( u ) in model M is defined as the solution for Y in the “surgically modified” submodel M x .

We see that the unit-level counterfactual Y x ( u ), which in the Neyman-Rubin approach is treated as a primitive, undefined quantity, is actually a derived quantity in the structural framework. The fact that we equate the experimental unit u with a vector of background conditions, U = u , in M , reflects the understanding that the name of a unit or its identity do not matter; it is only the vector U = u of attributes characterizing a unit which determines its behavior or response. As we go from one unit to another, the laws of nature, as they are reflected in the functions f X , f Y , etc. remain invariant; only the attributes U = u vary from individual to individual. 10

To illustrate, consider the solution of Y in the modified model M x 0 of Eq. (6) , which Definition 6 endows with the symbol Y x 0 ( u X , u Y , u Z ). This entity has a clear counterfactual interpretation, for it stands for the way an individual with characteristics ( u X , u Y , u Z ) would respond, had the treatment been x 0 , rather than the treatment x = f X ( z , u X ) actually received by that individual. In our example, since Y does not depend on u X and u Z , we can write:

In a similar fashion, we can derive

and so on. These examples reveal the counterfactual reading of each individual structural equation in the model of Eq. (5) . The equation x = f X ( z , u X ), for example, advertises the empirical claim that, regardless of the values taken by other variables in the system, had Z been z 0 , X would take on no other value but x = f X ( z 0 , u X ).

Clearly, the distribution P ( u Y , u X , u Z ) induces a well defined probability on the counterfactual event Y x 0 = y , as well as on joint counterfactual events, such as ‘ Y x 0 = y AND Y x 1 = y ′ ,’ which are, in principle, unobservable if x 0 ≠ x 1 . Thus, to answer attributional questions, such as whether Y would be y 1 if X were x 1 , given that in fact Y is y 0 and X is x 0 , we need to compute the conditional probability P ( Y x 1 = y 1 | Y = y 0 , X = x 0 ) which is well defined once we know the forms of the structural equations and the distribution of the exogenous variables in the model. For example, assuming linear equations (as in Fig. 1 ),

the conditioning events Y = y 0 and X = x 0 yield U X = x 0 and U Y = y 0 − βx 0 , and we can conclude that, with probability one, Y x 1 must take on the value: Y x 1 = βx 1 + U Y = β ( x 1 − x 0 ) + y 0 . In other words, if X were x 1 instead of x 0 , Y would increase by β times the difference ( x 1 − x 0 ). In nonlinear systems, the result would also depend on the distribution of { U X , U Y } and, for that reason, attributional queries are generally not identifiable in nonparametric models (see Section 6.3 and 2000a, Chapter 9).

In general, if x and x ′ are incompatible then Y x and Y x ′ cannot be measured simultaneously, and it may seem meaningless to attribute probability to the joint statement “ Y would be y if X = x and Y would be y ′ if X = x ′ .” 11 Such concerns have been a source of objections to treating counterfactuals as jointly distributed random variables ( Dawid, 2000 ). The definition of Y x and Y x ′ in terms of two distinct submodels neutralizes these objections ( Pearl, 2000b ), since the contradictory joint statement is mapped into an ordinary event, one where the background variables satisfy both statements simultaneously, each in its own distinct submodel; such events have well defined probabilities.

The surgical definition of counterfactuals given by (29), provides the conceptual and formal basis for the Neyman-Rubin potential-outcome framework, an approach to causation that takes a controlled randomized trial (CRT) as its ruling paradigm, assuming that nothing is known to the experimenter about the science behind the data. This “black-box” approach, which has thus far been denied the benefits of graphical or structural analyses, was developed by statisticians who found it difficult to cross the two mental barriers discussed in Section 2.2. Section 5 establishes the precise relationship between the structural and potential-outcome paradigms, and outlines how the latter can benefit from the richer representational power of the former.

4. Methodological Principles of Causal Inference

The structural theory described in the previous sections dictates a principled methodology that eliminates much of the confusion concerning the interpretations of study results as well as the ethical dilemmas that this confusion tends to spawn. The methodology dictates that every investigation involving causal relationships (and this entails the vast majority of empirical studies in the health, social, and behavioral sciences) should be structured along the following four-step process:

• Define: Express the target quantity Q as a function Q ( M ) that can be computed from any model M .
• Assume: Formulate causal assumptions using ordinary scientific language and represent their structural part in graphical form.
• Identify: Determine if the target quantity is identifiable (i.e., expressible in terms of estimable parameters).
• Estimate: Estimate the target quantity if it is identifiable, or approximate it, if it is not. Test the statistical implications of the model, if any, and modify the model when failure occurs.

4.1. Defining the target quantity

The definitional phase is the most neglected step in current practice of quantitative analysis. The structural modeling approach insists on defining the target quantity, be it “causal effect,” “mediated effect,” “effect on the treated,” or “probability of causation” before specifying any aspect of the model, without making functional or distributional assumptions and prior to choosing a method of estimation.

The investigator should view this definition as an algorithm that receives a model M as an input and delivers the desired quantity Q ( M ) as the output. Surely, such algorithm should not be tailored to any aspect of the input M ; it should be general, and ready to accommodate any conceivable model M whatsoever. Moreover, the investigator should imagine that the input M is a completely specified model, with all the functions f X , f Y , . . . and all the U variables (or their associated probabilities) given precisely. This is the hardest step for statistically trained investigators to make; knowing in advance that such model details will never be estimable from the data, the definition of Q ( M ) appears like a futile exercise in fantasy land – it is not.

For example, the formal definition of the causal effect P ( y | do ( x )), as given in Eq. (7) , is universally applicable to all models, parametric as well as nonparametric, through the formation of a submodel M x . By defining causal effect procedurally, thus divorcing it from its traditional parametric representation, the structural theory avoids the many pitfalls and confusions that have plagued the interpretation of structural and regressional parameters for the past half century. 12

4.2. Explicating causal assumptions

This is the second most neglected step in causal analysis. In the past, the difficulty has been the lack of a language suitable for articulating causal assumptions which, aside from impeding investigators from explicating assumptions, also inhibited them from giving causal interpretations to their findings.

Structural equation models, in their counterfactual reading, have removed this lingering difficulty by providing the needed language for causal analysis. Figures 3 and ​ and4 4 illustrate the graphical component of this language, where assumptions are conveyed through the missing arrows in the diagram. If numerical or functional knowledge is available, for example, linearity or monotonicity of the functions f X , f Y , . . ., those are stated separately, and applied in the identification and estimation phases of the study. Today we understand that the longevity and natural appeal of structural equations stem from the fact that they permit investigators to communicate causal assumptions formally and in the very same vocabulary in which scientific knowledge is stored.

Unfortunately, however, this understanding is not shared by all causal analysts; some analysts vehemently oppose the re-emergence of structure-based causation and insist, instead, on articulating causal assumptions exclusively in the unnatural (though formally equivalent) language of “potential outcomes,” “ignorability,” “missing data,” “treatment assignment,” and other metaphors borrowed from clinical trials. This modern assault on structural models is perhaps more dangerous than the regressional invasion that distorted the causal readings of these models in the late 1970s ( Richard, 1980 ). While sanctioning causal inference in one idiosyncratic style of analysis, the modern assault denies validity to any other style, including structural equations, thus discouraging investigators from subjecting models to the scrutiny of scientific knowledge.

This exclusivist attitude is manifested in passages such as: “The crucial idea is to set up the causal inference problem as one of missing data” or “If a problem of causal inference cannot be formulated in this manner (as the comparison of potential outcomes under different treatment assignments), it is not a problem of inference for causal effects, and the use of “causal” should be avoided,” or, even more bluntly, “the underlying assumptions needed to justify any causal conclusions should be carefully and explicitly argued, not in terms of technical properties like “uncorrelated error terms,” but in terms of real world properties, such as how the units received the different treatments” ( Wilkinson, the Task Force on Statistical Inference, and APA Board of Scientific Affairs , 1999 ).

The methodology expounded in this paper testifies against such restrictions. It demonstrates the viability and scientific soundness of the traditional structural equations paradigm, which stands diametrically opposed to the “missing data” paradigm. It renders the vocabulary of “treatment assignment” stifling and irrelevant (e.g., there is no “treatment assignment” in sex discrimination cases). Most importantly, it strongly prefers the use of “uncorrelated error terms,” (or “omitted factors”) over its “strong ignorability” alternative, as the proper way of articulating causal assumptions. Even the most devout advocates of the “strong ignorability” language use “omitted factors” when the need arises to defend assumptions (e.g., ( Sobel, 2008 ))

4.3. Identification, estimation, and approximation

Having unburden itself from parametric representations, the identification process in the structural framework proceeds either in the space of assumptions (i.e., the diagram) or in the space of mathematical expressions, after translating the graphical assumptions into a counterfactual language, as demonstrated in Section 5.3. Graphical criteria such as those of Definition 3 and Theorem 3 permit the identification of causal effects to be decided entirely within the graphical domain, where it can benefit from the guidance of scientific understanding. Identification of counterfactual queries, on the other hand, often require a symbiosis of both algebraic and graphical techniques. The nonparametric nature of the identification task (Definition 1) makes it clear that contrary to traditional folklore in linear analysis, it is not the model that need be identified but the query Q – the target of investigation. It also provides a simple way of proving non-identifiability: the construction of two parameterization of M , agreeing in P and disagreeing in Q , is sufficient to rule out identifiability.

When Q is identifiable, the structural framework also delivers an algebraic expression for the estimand EST ( Q ) of the target quantity Q , examples of which are given in Eqs. (24) and (25) , and estimation techniques are then unleashed as discussed in Section 3.3.4. An integral part of this estimation phase is a test for the testable implications, if any, of those assumptions in M that render Q identifiable – there is no point in estimating EST ( Q ) if the data proves those assumptions false and EST ( Q ) turns out to be a misrepresentation of Q . Investigators should be reminded, however, that only a fraction, called “kernel,” of the assumptions embodied in M are needed for identifying Q ( Pearl, 2004 ), the rest may be violated in the data with no effect on Q . In Fig. 2 , for example, the assumption { U Z ⊥⊥ U X } is not necessary for identifying Q = P ( y | do ( x )); the kernel { U Y ⊥⊥ U Z , U Y ⊥⊥ U X } (together with the missing arrows) is sufficient. Therefore, the testable implication of this kernel, Z ⊥⊥ Y | X , is all we need to test when our target quantity is Q ; the assumption { U Z ⊥⊥ U X } need not concern us.

More importantly, investigators must keep in mind that only a tiny fraction of any kernel lends itself to statistical tests, the bulk of it must remain untestable, at the mercy of scientific judgment. In Fig. 2 , for example, the assumption set { U X ⊥⊥ U Z , U Y ⊥⊥ U X } constitutes a sufficient kernel for Q = P ( y | do ( x )) (see Eq. (28) ) yet it has no testable implications whatsoever. The prevailing practice of submitting an entire structural equation model to a “goodness of fit” test ( Bollen, 1989 ) in support of causal claims is at odd with the logic of SCM (see ( Pearl, 2000a , pp. 144–5)). Alternative causal models usually exist that make contradictory claims and, yet, possess identical statistical implications. Statistical test can be used for rejecting certain kernels, in the rare cases where such kernels have testable implications, but the lion’s share of supporting causal claims falls on the shoulders of untested causal assumptions.

When conditions for identification are not met, the best one can do is derive bounds for the quantities of interest—namely, a range of possible values of Q that represents our ignorance about the details of the data-generating process M and that cannot be improved with increasing sample size. A classical example of non identifiable model that has been approximated by bounds, is the problem of estimating causal effect in experimental studies marred by non compliance, the structure of which is given in Fig. 5 .

Our task in this example is to find the highest and lowest values of Q

subject to the equality constraints imposed by the observed probabilities P ( x , y , | z ), where the maximization ranges over all possible functions P ( u Y , u X ), P ( y | x , u X ) and P ( x | z , u Y ) that satisfy those constraints.

Realizing that units in this example fall into 16 equivalence classes, each representing a binary function X = f ( z ) paired with a binary function y = g ( x ), Balke and Pearl (1997) were able to derive closed-form solutions for these bounds. 13 They showed that, in certain cases, the derived bounds can yield significant information on the treatment efficacy. Chickering and Pearl (1997) further used Bayesian techniques (with Gibbs sampling) to investigate the sharpness of these bounds as a function of sample size. Kaufman, Kaufman, and MacLenose (2009) used this technique to bound direct and indirect effects (see Section 6.1).

5. The Potential Outcome Framework

This section compares the structural theory presented in Sections 1–3 to the potential-outcome framework, usually associated with the names of Neyman (1923) and Rubin (1974) , which takes the randomized experiment as its ruling paradigm and has appealed therefore to researchers who do not find that paradigm overly constraining. This framework is not a contender for a comprehensive theory of causation for it is subsumed by the structural theory and excludes ordinary cause-effect relationships from its assumption vocabulary. We here explicate the logical foundation of the Neyman-Rubin framework, its formal subsumption by the structural causal model, and how it can benefit from the insights provided by the broader perspective of the structural theory.

The primitive object of analysis in the potential-outcome framework is the unit-based response variable, denoted Y x ( u ), read: “the value that outcome Y would obtain in experimental unit u , had treatment X been x .” Here, unit may stand for an individual patient, an experimental subject, or an agricultural plot. In Section 3.4 ( Eq. (29) we saw that this counterfactual entity has a natural interpretation in the SCM; it is the solution for Y in a modified system of equations, where unit is interpreted a vector u of background factors that characterize an experimental unit. Each structural equation model thus carries a collection of assumptions about the behavior of hypothetical units, and these assumptions permit us to derive the counterfactual quantities of interest. In the potential-outcome framework, however, no equations are available for guidance and Y x ( u ) is taken as primitive, that is, an undefined quantity in terms of which other quantities are defined; not a quantity that can be derived from the model. In this sense the structural interpretation of Y x ( u ) given in (29) provides the formal basis for the potential-outcome approach; the formation of the submodel M x explicates mathematically how the hypothetical condition “had X been x ” is realized, and what the logical consequences are of such a condition.

5.1. The “black-box” missing-data paradigm

The distinct characteristic of the potential-outcome approach is that, although investigators must think and communicate in terms of undefined, hypothetical quantities such as Y x ( u ), the analysis itself is conducted almost entirely within the axiomatic framework of probability theory. This is accomplished, by postulating a “super” probability function on both hypothetical and real events. If U is treated as a random variable then the value of the counterfactual Y x ( u ) becomes a random variable as well, denoted as Y x . The potential-outcome analysis proceeds by treating the observed distribution P ( x 1 , . . ., x n ) as the marginal distribution of an augmented probability function P* defined over both observed and counterfactual variables. Queries about causal effects (written P ( y | do ( x )) in the structural analysis) are phrased as queries about the marginal distribution of the counterfactual variable of interest, written P *( Y x = y ). The new hypothetical entities Y x are treated as ordinary random variables; for example, they are assumed to obey the axioms of probability calculus, the laws of conditioning, and the axioms of conditional independence.

Naturally, these hypothetical entities are not entirely whimsy. They are assumed to be connected to observed variables via consistency constraints ( Robins, 1986 ) such as

which states that, for every u , if the actual value of X turns out to be x , then the value that Y would take on if ‘ X were x ’ is equal to the actual value of Y . For example, a person who chose treatment x and recovered, would also have recovered if given treatment x by design. When X is binary, it is sometimes more convenient to write (32) as:

Whether additional constraints should tie the observables to the unobservables is not a question that can be answered in the potential-outcome framework; for it lacks an underlying model to define its axioms.

The main conceptual difference between the two approaches is that, whereas the structural approach views the intervention do ( x ) as an operation that changes a distribution but keeps the variables the same, the potential-outcome approach views the variable Y under do ( x ) to be a different variable, Y x , loosely connected to Y through relations such as (32), but remaining unobserved whenever X ≠ x . The problem of inferring probabilistic properties of Y x , then becomes one of “missing-data” for which estimation techniques have been developed in the statistical literature.

Pearl (2000a , Chapter 7) shows, using the structural interpretation of Y x ( u ), that it is indeed legitimate to treat counterfactuals as jointly distributed random variables in all respects, that consistency constraints like (32) are automatically satisfied in the structural interpretation and, moreover, that investigators need not be concerned about any additional constraints except the following two

Equation (33) ensures that the interventions do ( Y = y ) results in the condition Y = y , regardless of concurrent interventions, say do ( Z = z ), that may be applied to variables other than Y . Equation (34) generalizes (32) to cases where Z is held fixed, at z . (See ( Halpern, 1998 ) for proof of completeness.)

5.2. Problem formulation and the demystification of “ignorability”

The main drawback of this black-box approach surfaces in problem formulation, namely, the phase where a researcher begins to articulate the “science” or “causal assumptions” behind the problem of interest. Such knowledge, as we have seen in Section 1, must be articulated at the onset of every problem in causal analysis – causal conclusions are only as valid as the causal assumptions upon which they rest.

To communicate scientific knowledge, the potential-outcome analyst must express assumptions as constraints on P* , usually in the form of conditional independence assertions involving counterfactual variables. For instance, in our example of Fig. 5 , to communicate the understanding that Z is randomized (hence independent of U X and U Y ), the potential-outcome analyst would use the independence constraint Z ⊥⊥{ Y z 1 , Y z 2 , . . ., Y z k }. 14 To further formulate the understanding that Z does not affect Y directly, except through X , the analyst would write a, so called, “exclusion restriction”: Y xz = Y x .

A collection of constraints of this type might sometimes be sufficient to permit a unique solution to the query of interest. For example, if one can plausibly assume that, in Fig. 4 , a set Z of covariates satisfies the conditional independence

(an assumption termed “conditional ignorability” by Rosenbaum and Rubin (1983) ,) then the causal effect P ( y | do ( x )) = P* ( Y x = y ) can readily be evaluated to yield

The last expression contains no counterfactual quantities (thus permitting us to drop the asterisk from P* ) and coincides precisely with the standard covariate-adjustment formula of Eq. (25) .

We see that the assumption of conditional ignorability (35) qualifies Z as an admissible covariate for adjustment; it mirrors therefore the “back-door” criterion of Definition 3, which bases the admissibility of Z on an explicit causal structure encoded in the diagram.

The derivation above may explain why the potential-outcome approach appeals to mathematical statisticians; instead of constructing new vocabulary (e.g., arrows), new operators ( do ( x )) and new logic for causal analysis, almost all mathematical operations in this framework are conducted within the safe confines of probability calculus. Save for an occasional application of rule (34) or (32)), the analyst may forget that Y x stands for a counterfactual quantity—it is treated as any other random variable, and the entire derivation follows the course of routine probability exercises.

This orthodoxy exacts a high cost: Instead of bringing the theory to the problem, the problem must be reformulated to fit the theory; all background knowledge pertaining to a given problem must first be translated into the language of counterfactuals (e.g., ignorability conditions) before analysis can commence. This translation may in fact be the hardest part of the problem. The reader may appreciate this aspect by attempting to judge whether the assumption of conditional ignorability (35), the key to the derivation of (36), holds in any familiar situation, say in the experimental setup of Fig. 2(a) . This assumption reads: “the value that Y would obtain had X been x , is independent of X , given Z ”. Even the most experienced potential-outcome expert would be unable to discern whether any subset Z of covariates in Fig. 4 would satisfy this conditional independence condition. 15 Likewise, to derive Eq. (35) in the language of potential-outcome (see ( Pearl, 2000a , p. 223)), one would need to convey the structure of the chain X → W 3 → Y using the cryptic expression: W 3 x ⊥⊥{ Y w 3 , X }, read: “the value that W 3 would obtain had X been x is independent of the value that Y would obtain had W 3 been w 3 jointly with the value of X .” Such assumptions are cast in a language so far removed from ordinary understanding of scientific theories that, for all practical purposes, they cannot be comprehended or ascertained by ordinary mortals. As a result, researchers in the graph-less potential-outcome camp rarely use “conditional ignorability” (35) to guide the choice of covariates; they view this condition as a hoped-for miracle of nature rather than a target to be achieved by reasoned design. 16

Replacing “ignorability” with a conceptually meaningful condition (i.e., back-door) in a graphical model permits researchers to understand what conditions covariates must fulfill before they eliminate bias, what to watch for and what to think about when covariates are selected, and what experiments we can do to test, at least partially, if we have the knowledge needed for covariate selection.

Aside from offering no guidance in covariate selection, formulating a problem in the potential-outcome language encounters three additional hurdles. When counterfactual variables are not viewed as byproducts of a deeper, process-based model, it is hard to ascertain whether all relevant judgments have been articulated, whether the judgments articulated are redundant , or whether those judgments are self-consistent. The need to express, defend, and manage formidable counterfactual relationships of this type explain the slow acceptance of causal analysis among health scientists and statisticians, and why most economists and social scientists continue to use structural equation models ( Wooldridge, 2002 , Stock and Watson, 2003 , Heckman, 2008 ) instead of the potential-outcome alternatives advocated in Angrist, Imbens, and Rubin (1996) , Holland (1988) , Sobel (1998 , 2008) .

On the other hand, the algebraic machinery offered by the counterfactual notation, Y x ( u ), once a problem is properly formalized, can be extremely powerful in refining assumptions ( Angrist et al., 1996 , Heckman and Vytlacil, 2005 ), deriving consistent estimands ( Robins, 1986 ), bounding probabilities of necessary and sufficient causation ( Tian and Pearl, 2000 ), and combining data from experimental and nonexperimental studies ( Pearl, 2000a ). The next subsection (5.3) presents a way of combining the best features of the two approaches. It is based on encoding causal assumptions in the language of diagrams, translating these assumptions into counterfactual notation, performing the mathematics in the algebraic language of counterfactuals (using (32), (33), and (34)) and, finally, interpreting the result in graphical terms or plain causal language. The mediation problem of Section 6.1 illustrates how such symbiosis clarifies the definition and identification of direct and indirect effects, 17 and how it overcomes difficulties that were deemed insurmountable in the exclusivist potential-outcome framework ( Rubin, 2004 , 2005 ).

5.3. Combining graphs and potential outcomes

The formulation of causal assumptions using graphs was discussed in Section 3. In this subsection we will systematize the translation of these assumptions from graphs to counterfactual notation.

Structural equation models embody causal information in both the equations and the probability function P ( u ) assigned to the exogenous variables; the former is encoded as missing arrows in the diagrams the latter as missing (double arrows) dashed arcs. Each parent-child family ( PA i , X i ) in a causal diagram G corresponds to an equation in the model M . Hence, missing arrows encode exclusion assumptions, that is, claims that manipulating variables that are excluded from an equation will not change the outcome of the hypothetical experiment described by that equation. Missing dashed arcs encode independencies among error terms in two or more equations. For example, the absence of dashed arcs between a node Y and a set of nodes { Z 1 , . . ., Z k } implies that the corresponding background variables, U Y and { U Z 1 , . . ., U Z k }, are independent in P ( u ).

These assumptions can be translated into the potential-outcome notation using two simple rules ( Pearl, 2000a , p. 232); the first interprets the missing arrows in the graph, the second, the missing dashed arcs.

• Exclusion restrictions: For every variable Y having parents PA Y and for every set of endogenous variables S disjoint of PA Y , we have Y p a Y =  Y p a Y , s . (37)
• Independence restrictions: If Z 1 , . . ., Z k is any set of nodes not connected to Y via dashed arcs, and PA 1 , . . ., PA k their respective sets of parents, we have Y p a Y  ⊥  ⊥ { Z 1   p a 1 , …,  Z k    p a k }. (38)

The exclusion restrictions expresses the fact that each parent set includes all direct causes of the child variable, hence, fixing the parents of Y , determines the value of Y uniquely, and intervention on any other set S of (endogenous) variables can no longer affect Y . The independence restriction translates the independence between U Y and { U Z 1 , . . ., U Z k } into independence between the corresponding potential-outcome variables. This follows from the observation that, once we set their parents, the variables in { Y , Z 1 , . . ., Z k } stand in functional relationships to the U terms in their corresponding equations.

As an example, consider the model shown in Fig. 5 , which serves as the canonical representation for the analysis of instrumental variables ( Angrist et al., 1996 , Balke and Pearl, 1997 ). This model displays the following parent sets:

Consequently, the exclusion restrictions translate into:

the absence of any dashed arc between Z and { Y , X } translates into the independence restriction

This is precisely the condition of randomization; Z is independent of all its non-descendants, namely independent of U X and U Y which are the exogenous parents of Y and X , respectively. (Recall that the exogenous parents of any variable, say Y , may be replaced by the counterfactual variable Y pa Y , because holding PA Y constant renders Y a deterministic function of its exogenous parent U Y .)

The role of graphs is not ended with the formulation of causal assumptions. Throughout an algebraic derivation, like the one shown in Eq. (36) , the analyst may need to employ additional assumptions that are entailed by the original exclusion and independence assumptions, yet are not shown explicitly in their respective algebraic expressions. For example, it is hardly straightforward to show that the assumptions of Eqs. (40) – (41) imply the conditional independence ( Y x ⊥⊥ Z |{ X z , X }) but do not imply the conditional independence ( Y x ⊥⊥ Z | X ). These are not easily derived by algebraic means alone. Such implications can, however, easily be tested in the graph of Fig. 5 using the graphical reading for conditional independence (Definition 1). (See ( Pearl, 2000a , pp. 16–17, 213–215).) Thus, when the need arises to employ independencies in the course of a derivation, the graph may assist the procedure by vividly displaying the independencies that logically follow from our assumptions.

6. Counterfactuals at Work

6.1. mediation: direct and indirect effects, 6.1.1. direct versus total effects.

The causal effect we have analyzed so far, P ( y | do ( x )), measures the total effect of a variable (or a set of variables) X on a response variable Y . In many cases, this quantity does not adequately represent the target of investigation and attention is focused instead on the direct effect of X on Y . The term “direct effect” is meant to quantify an effect that is not mediated by other variables in the model or, more accurately, the sensitivity of Y to changes in X while all other factors in the analysis are held fixed. Naturally, holding those factors fixed would sever all causal paths from X to Y with the exception of the direct link X → Y , which is not intercepted by any intermediaries.

A classical example of the ubiquity of direct effects involves legal disputes over race or sex discrimination in hiring. Here, neither the effect of sex or race on applicants’ qualification nor the effect of qualification on hiring are targets of litigation. Rather, defendants must prove that sex and race do not directly influence hiring decisions, whatever indirect effects they might have on hiring by way of applicant qualification.

From a policy making viewpoint, an investigator may be interested in decomposing effects to quantify the extent to which racial salary disparity is due to educational disparity, or, taking a health-care example, the extent to which sensitivity to a given exposure can be reduced by eliminating sensitivity to an intermediate factor, standing between exposure and outcome. Another example concerns the identification of neural pathways in the brain or the structural features of protein-signaling networks in molecular biology ( Brent and Lok, 2005 ). Here, the decomposition of effects into their direct and indirect components carries theoretical scientific importance, for it tells us “how nature works” and, therefore, enables us to predict behavior under a rich variety of conditions.

Yet despite its ubiquity, the analysis of mediation has long been a thorny issue in the social and behavioral sciences ( Judd and Kenny, 1981 , Baron and Kenny, 1986 , Muller, Judd, and Yzerbyt, 2005 , Shrout and Bolger, 2002 , MacKinnon, Fairchild, and Fritz, 2007a ) primarily because structural equation modeling in those sciences were deeply entrenched in linear analysis, where the distinction between causal parameters and their regressional interpretations can easily be conflated. 18 As demands grew to tackle problems involving binary and categorical variables, researchers could no longer define direct and indirect effects in terms of structural or regressional coefficients, and all attempts to extend the linear paradigms of effect decomposition to non-linear systems produced distorted results ( MacKinnon, Lockwood, Brown, Wang, and Hoffman, 2007b ). These difficulties have accentuated the need to redefine and derive causal effects from first principles, uncommitted to distributional assumptions or a particular parametric form of the equations. The structural methodology presented in this paper adheres to this philosophy and it has produced indeed a principled solution to the mediation problem, based on the counterfactual reading of structural equations (29) . The following subsections summarize the method and its solution.

6.1.2. Controlled direct-effects

A major impediment to progress in mediation analysis has been the lack of notational facility for expressing the key notion of “holding the mediating variables fixed” in the definition of direct effect. Clearly, this notion must be interpreted as (hypothetically) setting the intermediate variables to constants by physical intervention, not by analytical means such as selection, regression, conditioning, matching or adjustment. For example, consider the simple mediation models of Fig. 6 , where the error terms (not shown explicitly) are assumed to be independent. It will not be sufficient to measure the association between gender ( X ) and hiring ( Y ) for a given level of qualification ( Z ), (see Fig. 6(b) ) because, by conditioning on the mediator Z , we create spurious associations between X and Y through W 2 , even when there is no direct effect of X on Y ( Pearl, 1998 , Cole and Hernán, 2002 ).

(a) A generic model depicting mediation through Z with no confounders, and (b) with two confounders, W 1 and W 2 .

Using the do ( x ) notation, enables us to correctly express the notion of “holding Z fixed” and obtain a simple definition of the controlled direct effect of the transition from X = x to X = x ′ :

or, equivalently, using counterfactual notation:

where Z is the set of all mediating variables. The readers can easily verify that, in linear systems, the controlled direct effect reduces to the path coefficient of the link X → Y (see footnote 12 ) regardless of whether confounders are present (as in Fig. 6(b) ) and regardless of whether the error terms are correlated or not.

This separates the task of definition from that of identification, as demanded by Section 4.1. The identification of CDE would depend, of course, on whether confounders are present and whether they can be neutralized by adjustment, but these do not alter its definition. Nor should trepidation about infeasibility of the action do ( gender = male ) enter the definitional phase of the study, Definitions apply to symbolic models, not to human biology. Graphical identification conditions for expressions of the type E ( Y | do ( x ), do ( z 1 ), do ( z 2 ), . . ., do ( z k )) in the presence of unmeasured confounders were derived by Pearl and Robins (1995) (see Pearl (2000a , Chapter 4) and invoke sequential application of the back-door conditions discussed in Section 3.2.

6.1.3. Natural direct effects

In linear systems, the direct effect is fully specified by the path coefficient attached to the link from X to Y ; therefore, the direct effect is independent of the values at which we hold Z . In nonlinear systems, those values would, in general, modify the effect of X on Y and thus should be chosen carefully to represent the target policy under analysis. For example, it is not uncommon to find employers who prefer males for the high-paying jobs (i.e., high z ) and females for low-paying jobs (low z ).

When the direct effect is sensitive to the levels at which we hold Z , it is often more meaningful to define the direct effect relative to some “natural” base-line level that may vary from individual to individual, and represents the level of Z just before the change in X . Conceptually, we can define the natural direct effect DE x,x ′ ( Y ) as the expected change in Y induced by changing X from x to x ′ while keeping all mediating factors constant at whatever value they would have obtained under do ( x ). This hypothetical change, which Robins and Greenland (1992) conceived and called “pure” and Pearl (2001) formalized and analyzed under the rubric “natural,” mirrors what lawmakers instruct us to consider in race or sex discrimination cases: “The central question in any employment-discrimination case is whether the employer would have taken the same action had the employee been of a different race (age, sex, religion, national origin etc.) and everything else had been the same.” (In Carson versus Bethlehem Steel Corp. , 70 FEP Cases 921, 7th Cir. (1996)).

Extending the subscript notation to express nested counterfactuals, Pearl (2001) gave a formal definition for the “natural direct effect”:

Here, Y x ′ , Z x represents the value that Y would attain under the operation of setting X to x ′ and, simultaneously, setting Z to whatever value it would have obtained under the setting X = x . We see that DE x,x′ ( Y ), the natural direct effect of the transition from x to x ′ , involves probabilities of nested counterfactuals and cannot be written in terms of the do ( x ) operator. Therefore, the natural direct effect cannot in general be identified, even with the help of ideal, controlled experiments (see footnote 8 for intuitive explanation). However, aided by the surgical definition of Eq. (29) and the notational power of nested counterfactuals, Pearl (2001) was nevertheless able to show that, if certain assumptions of “no confounding” are deemed valid, the natural direct effect can be reduced to

The intuition is simple; the natural direct effect is the weighted average of the controlled direct effect, using the causal effect P ( z | do ( x )) as a weighing function.

One condition for the validity of (43) is that Z x ⊥⊥ Y x′,z | W holds for some set W of measured covariates. This technical condition in itself, like the ignorability condition of (35), is close to meaningless for most investigators, as it is not phrased in terms of realized variables. The surgical interpretation of counterfactuals (29) can be invoked at this point to unveil the graphical interpretation of this condition. It states that W should be admissible (i.e., satisfy the back-door condition) relative the path(s) from Z to Y . This condition, satisfied by W 2 in Fig. 6(b) , is readily comprehended by empirical researchers, and the task of selecting such measurements, W , can then be guided by the available scientific knowledge. Additional graphical and counterfactual conditions for identification are derived in Pearl (2001) Petersen et al. (2006) and Imai, Keele, and Yamamoto (2008) .

In particular, it can be shown ( Pearl, 2001 ) that expression (43) is both valid and identifiable in Markovian models (i.e., no unobserved confounders) where each term on the right can be reduced to a “ do -free” expression using Eq. (24) or (25) and then estimated by regression.

For example, for the model in Fig. 6(b) , Eq. (43) reads:

while for the confounding-free model of Fig. 6(a) we have:

Both (44) and (45) can easily be estimated by a two-step regression.

6.1.4. Natural indirect effects

Remarkably, the definition of the natural direct effect (42) can be turned around and provide an operational definition for the indirect effect – a concept shrouded in mystery and controversy, because it is impossible, using the do ( x ) operator, to disable the direct link from X to Y so as to let X influence Y solely via indirect paths.

The natural indirect effect , IE , of the transition from x to x ′ is defined as the expected change in Y affected by holding X constant, at X = x , and changing Z to whatever value it would have attained had X been set to X = x ′ . Formally, this reads ( Pearl, 2001 ):

which is almost identical to the direct effect ( Eq. (42) ) save for exchanging x and x ′ in the first term.

Indeed, it can be shown that, in general, the total effect TE of a transition is equal to the difference between the direct effect of that transition and the indirect effect of the reverse transition. Formally,

In linear systems, where reversal of transitions amounts to negating the signs of their effects, we have the standard additive formula

Since each term above is based on an independent operational definition, this equality constitutes a formal justification for the additive formula used routinely in linear systems.

Note that, although it cannot be expressed in do -notation, the indirect effect has clear policy-making implications. For example: in the hiring discrimination context, a policy maker may be interested in predicting the gender mix in the work force if gender bias is eliminated and all applicants are treated equally—say, the same way that males are currently treated. This quantity will be given by the indirect effect of gender on hiring, mediated by factors such as education and aptitude, which may be gender-dependent.

More generally, a policy maker may be interested in the effect of issuing a directive to a select set of subordinate employees, or in carefully controlling the routing of messages in a network of interacting agents. Such applications motivate the analysis of path-specific effects , that is, the effect of X on Y through a selected set of paths ( Avin, Shpitser, and Pearl, 2005 ).

In all these cases, the policy intervention invokes the selection of signals to be sensed, rather than variables to be fixed. Pearl (2001) has suggested therefore that signal sensing is more fundamental to the notion of causation than manipulation ; the latter being but a crude way of stimulating the former in experimental setup. The mantra “No causation without manipulation” must be rejected. (See ( Pearl, 2009b , Section 11.4.5).)

It is remarkable that counterfactual quantities like DE and IE that could not be expressed in terms of do ( x ) operators, and appear therefore void of empirical content, can, under certain conditions be estimated from empirical studies, and serve to guide policies. Awareness of this potential should embolden researchers to go through the definitional step of the study and freely articulate the target quantity Q ( M ) in the language of science, i.e., counterfactuals, despite the seemingly speculative nature of each assumption in the model ( Pearl, 2000b ).

6.2. The Mediation Formula: a simple solution to a thorny problem

This subsection demonstrates how the solution provided in equations (45) and (48) can be applied to practical problems of assessing mediation effects in non-linear models. We will use the simple mediation model of Fig. 6(a) , where all error terms (not shown explicitly) are assumed to be mutually independent, with the understanding that adjustment for appropriate sets of covariates W may be necessary to achieve this independence and that integrals should replace summations when dealing with continuous variables ( Imai et al., 2008 ).

Combining (45) and (48), the expression for the indirect effect, IE , becomes:

which provides a general formula for mediation effects, applicable to any nonlinear system, any distribution (of U ), and any type of variables. Moreover, the formula is readily estimable by regression. Owed to its generality and ubiquity, I will refer to this expression as the “Mediation Formula.”

The Mediation Formula represents the average increase in the outcome Y that the transition from X = x to X = x ′ is expected to produce absent any direct effect of X on Y . Though based on solid causal principles, it embodies no causal assumption other than the generic mediation structure of Fig. 6(a) . When the outcome Y is binary (e.g., recovery, or hiring) the ratio (1 − IE / TE ) represents the fraction of responding individuals who owe their response to direct paths, while (1 − DE / TE ) represents the fraction who owe their response to Z -mediated paths.

The Mediation Formula tells us that IE depends only on the expectation of the counterfactual Y xz , not on its functional form f Y ( x , z , u Y ) or its distribution P ( Y xz = y ). It calls therefore for a two-step regression which, in principle, can be performed non-parametrically. In the first step we regress Y on X and Z , and obtain the estimate

for every ( x , z ) cell. In the second step we estimate the expectation of g ( x , z ) conditional on X = x ′ and X = x , respectively, and take the difference:

Nonparametric estimation is not always practical. When Z consists of a vector of several mediators, the dimensionality of the problem would prohibit the estimation of E ( Y | x , z ) for every ( x , z ) cell, and the need arises to use parametric approximation. We can then choose any convenient parametric form for E ( Y | x , z ) (e.g., linear, logit, probit), estimate the parameters separately (e.g., by regression or maximum likelihood methods), insert the parametric approximation into (49) and estimate its two conditional expectations (over z ) to get the mediated effect ( VanderWeele, 2009 ).

Let us examine what the Mediation Formula yields when applied to both linear and non-linear versions of model 6(a). In the linear case, the structural model reads:

Computing the conditional expectation in (49) gives

where b is the total effect coefficient, b = ( E ( Y | x ′ ) − E ( Y | x ))/( x ′ − x ) = c x + c z b x .

We thus obtained the standard expressions for indirect effects in linear systems, which can be estimated either as a difference in two regression coefficients ( Eq. 53 ) or a product of two regression coefficients ( Eq. 52 ), with Y regressed on both X and Z . (see ( MacKinnon et al., 2007b )). These two strategies do not generalize to non-linear system as we shall see next.

Suppose we apply (49) to a non-linear process ( Fig. 7 ) in which X, Y , and Z are binary variables, and Y and Z are given by the Boolean formula

Such disjunctive interaction would describe, for example, a disease Y that would be triggered either by X directly, if enabled by e x , or by Z , if enabled by e z . Let us further assume that e x , e z and e xz are three independent Bernoulli variables with probabilities p x , p z , and p xz , respectively.

Stochastic non-linear model of mediation. All variables are binary.

As investigators, we are not aware, of course, of these underlying mechanisms; all we know is that X , Y , and Z are binary, that Z is hypothesized to be a mediator, and that the assumption of nonconfoundedness permits us to use the Mediation Formula (49) for estimating the Z -mediated effect of X on Y . Assume that our plan is to conduct a nonparametric estimation of the terms in (49) over a very large sample drawn from P ( x , y.z ); it is interesting to ask what the asymptotic value of the Mediation Formula would be, as a function of the model parameters: p x , p z , and p xz .

From knowledge of the underlying mechanism, we have:

Taking x = 0, x ′ = 1 and substituting these expressions in (45), (48), and (49) yields

Two observations are worth noting. First, we see that, despite the non-linear interaction between the two causal paths, the parameters of one do not influence on the causal effect mediated by the other. Second, the total effect is not the sum of the direct and indirect effects. Instead, we have:

which means that a fraction DE · IE / TE of outcome cases triggered by the transition from X = 0 to X = 1 are triggered simultaneously, through both causal paths, and would have been triggered even if one of the paths was disabled.

Now assume that we choose to approximate E ( Y | x , z ) by the linear expression

After fitting the a ’s parameters to the data (e.g., by OLS) and substituting in (49) one would obtain

which holds whenever we use the approximation in (57), regardless of the underlying mechanism.

If the correct data-generating process was the linear model of (50), we would obtain the expected estimates a 2 = c z , E ( z | x ′ ) − E ( z | x ′ ) = b x ( x ′ − x ) and

If however we were to apply the approximation in (57) to data generated by the nonlinear model of Fig. 7 , a distorted solution would ensue; a 2 would evaluate to

E ( z | x ′ ) − E ( z | x ) would evaluate to p xz ( x ′ − x ), and (58) would yield the approximation

We see immediately that the result differs from the correct value p z p xz derived in (54). Whereas the approximate value depends on P ( x = 1), the correct value shows no such dependence, and rightly so; no causal effect should depend on the probability of the causal variable.

Fortunately, the analysis permits us to examine under what condition the distortion would be significant. Comparing (59) and (54) reveals that the approximate method always underestimates the indirect effect and the distortion is minimal for high values of P ( x = 1) and (1− p x ).

Had we chosen to include an interaction term in the approximation of E ( Y | x , z ), the correct result would obtain. To witness, writing

a 2 would evaluate to p z , a 3 to p x p z , and the correct result obtains through:

We see that, in addition to providing causally-sound estimates for mediation effects, the Mediation Formula also enables researchers to evaluate analytically the effectiveness of various parametric specifications relative to any assumed model. This type of analytical “sensitivity analysis” has been used extensively in statistics for parameter estimation, but could not be applied to mediation analysis, owed to the absence of an objective target quantity that captures the notion of indirect effect in both linear and non-linear systems, free of parametric assumptions. The Mediation Formula of Eq. (49) explicates this target quantity formally, and casts it in terms of estimable quantities.

The derivation of the Mediation Formula was facilitated by taking seriously the four steps of the structural methodology (Section 4) together with the graphical-counterfactual-structural symbiosis spawned by the surgical interpretation of counterfactuals ( Eq. (29) ).

In contrast, when the mediation problem is approached from an exclusivist potential-outcome viewpoint, void of the structural guidance of Eq. (29) , counterintuitive definitions ensue, carrying the label “principal stratification” ( Rubin, 2004 , 2005 ), which are at variance with common understanding of direct and indirect effects. For example, the direct effect is definable only in units absent of indirect effects. This means that a grandfather would be deemed to have no direct effect on his grandson’s behavior in families where he has had some effect on the father. This precludes from the analysis all typical families, in which a father and a grandfather have simultaneous, complementary influences on children’s upbringing. In linear systems, to take an even sharper example, the direct effect would be undefined whenever indirect paths exist from the cause to its effect. The emergence of such paradoxical conclusions underscores the wisdom, if not necessity of a symbiotic analysis, in which the counterfactual notation Y x ( u ) is governed by its structural definition, Eq. (29) . 19

6.3. Causes of effects and probabilities of causation

The likelihood that one event was the cause of another guides much of what we understand about the world (and how we act in it). For example, knowing whether it was the aspirin that cured my headache or the TV program I was watching would surely affect my future use of aspirin. Likewise, to take an example from common judicial standard, judgment in favor of a plaintiff should be made if and only if it is “more probable than not” that the damage would not have occurred but for the defendant’s action ( Robertson, 1997 ).

These two examples fall under the category of “causes of effects” because they concern situations in which we observe both the effect, Y = y , and the putative cause X = x and we are asked to assess, counterfactually, whether the former would have occurred absent the latter.

We have remarked earlier ( footnote 8 ) that counterfactual probabilities conditioned on the outcome cannot in general be identified from observational or even experimental studies. This does not mean however that such probabilities are useless or void of empirical content; the structural perspective may guide us in fact toward discovering the conditions under which they can be assessed from data, thus defining the empirical content of these counterfactuals.

Following the 4-step process of structural methodology – define, assume, identify, and estimate – our first step is to express the target quantity in counterfactual notation and verify that it is well defined, namely, that it can be computed unambiguously from any fully-specified causal model.

In our case, this step is simple. Assuming binary events, with X = x and Y = y representing treatment and outcome, respectively, and X = x ′ , Y = y ′ their negations, our target quantity can be formulated directly from the English sentence:

“Find the probability that Y would be y ′ had X been x ′ , given that, in reality, Y is actually y and X is x ,”

This counterfactual quantity, which Robins and Greenland (1989b) named “probability of causation” and Pearl (2000a , p. 296) named “probability of necessity” (PN), to be distinguished from two other nuances of “causation,” is certainly computable from any fully specified structural model, i.e., one in which P ( u ) and all functional relationships are given. This follows from the fact that every structural model defines a joint distribution of counterfactuals, through Eq. (29) .

Having written a formal expression for PN, Eq. (60) , we can move on to the formulation and identification phases and ask what assumptions would permit us to identify PN from empirical studies, be they observational, experimental or a combination thereof.

This problem was analyzed in Pearl (2000a , Chapter 9) and yielded the following results:

Theorem 4 If Y is monotonic relative to X, i.e., Y 1 ( u ) ≥ Y 0 ( u ) , then PN is identifiable whenever the causal effect P ( y | do ( x )) is identifiable and, moreover,

The first term on the r.h.s. of (61) is the familiar excess risk ratio (ERR) that epidemiologists have been using as a surrogate for PN in court cases ( Cole, 1997 , Robins and Greenland, 1989b ). The second term represents the correction needed to account for confounding bias, that is, P ( y | do ( x ′ )) ≠ P ( y | x ′ ).

This suggests that monotonicity and unconfoundedness were tacitly assumed by the many authors who proposed or derived ERR as a measure for the “fraction of exposed cases that are attributable to the exposure” ( Greenland, 1999 ).

Equation (61) thus provides a more refined measure of causation, which can be used in situations where the causal effect P ( y | do ( x )) can be estimated from either randomized trials or graph-assisted observational studies (e.g., through Theorem 3 or Eq. (25) ). It can also be shown ( Tian and Pearl, 2000 ) that the expression in (61) provides a lower bound for PN in the general, nonmonotonic case. (See also ( Robins and Greenland, 1989a ).) In particular, the tight upper and lower bounds on PN are given by:

It is worth noting that, in drug related litigation, it is not uncommon to obtain data from both experimental and observational studies. The former is usually available at the manufacturer or the agency that approved the drug for distribution (e.g., FDA), while the latter is easy to obtain by random surveys of the population. In such cases, the standard lower bound used by epidemiologists to establish legal responsibility, the Excess Risk Ratio, can be improved substantially using the corrective term of Eq. (61) . Likewise, the upper bound of Eq. (62) can be used to exonerate drug-makers from legal responsibility. Cai and Kuroki (2006) analyzed the statistical properties of PN.

Pearl (2000a , p. 302) shows that combining data from experimental and observational studies which, taken separately, may indicate no causal relations between X and Y , can nevertheless bring the lower bound of Eq. (62) to unity, thus implying causation with probability one .

Such extreme results dispel all fears and trepidations concerning the empirical content of counterfactuals ( Dawid, 2000 , Pearl, 2000b ). They demonstrate that a quantity PN which at first glance appears to be hypothetical, ill-defined, untestable and, hence, unworthy of scientific analysis is nevertheless definable, testable and, in certain cases, even identifiable. Moreover, the fact that, under certain combination of data, and making no assumptions whatsoever, an important legal claim such as “the plaintiff would be alive had he not taken the drug” can be ascertained with probability approaching one, is a remarkable tribute to formal analysis.

Another counterfactual quantity that has been fully characterized recently is the Effect of Treatment on the Treated (ETT):

ETT has been used in econometrics to evaluate the effectiveness of social programs on their participants ( Heckman, 1992 ) and has long been the target of research in epidemiology, where it came to be known as “the effect of exposure on the exposed,” or “standardized morbidity” ( Miettinen, 1974 ; Greenland and Robins, 1986 ).

Shpitser and Pearl (2009) have derived a complete characterization of those models in which ETT can be identified from either experimental or observational studies. They have shown that, despite its blatant counterfactual character, (e.g., “I just took an aspirin, perhaps I shouldn’t have?”) ETT can be evaluated from experimental studies in many, though not all cases. It can also be evaluated from observational studies whenever a sufficient set of covariates can be measured that satisfies the back-door criterion and, more generally, in a wide class of graphs that permit the identification of conditional interventions.

These results further illuminate the empirical content of counterfactuals and their essential role in causal analysis. They prove once again the triumph of logic and analysis over traditions that a-priori exclude from the analysis quantities that are not testable in isolation. Most of all, they demonstrate the effectiveness and viability of the scientific approach to causation whereby the dominant paradigm is to model the activities of Nature, rather than those of the experimenter. In contrast to the ruling paradigm of conservative statistics, we begin with relationships that we know in advance will never be estimated, tested or falsified. Only after assembling a host of such relationships and judging them to faithfully represent our theory about how Nature operates, we ask whether the parameter of interest, crisply defined in terms of those theoretical relationships, can be estimated consistently from empirical data and how. It often does, to the credit of progressive statistics.

7. Conclusions

Traditional statistics is strong in devising ways of describing data and inferring distributional parameters from sample. Causal inference requires two additional ingredients: a science-friendly language for articulating causal knowledge, and a mathematical machinery for processing that knowledge, combining it with data and drawing new causal conclusions about a phenomenon. This paper surveys recent advances in causal analysis from the unifying perspective of the structural theory of causation and shows how statistical methods can be supplemented with the needed ingredients. The theory invokes non-parametric structural equations models as a formal and meaningful language for defining causal quantities, formulating causal assumptions, testing identifiability, and explicating many concepts used in causal discourse. These include: randomization, intervention, direct and indirect effects, confounding, counterfactuals, and attribution. The algebraic component of the structural language coincides with the potential-outcome framework, and its graphical component embraces Wright’s method of path diagrams. When unified and synthesized, the two components offer statistical investigators a powerful and comprehensive methodology for empirical research.

1 By “untested” I mean untested using frequency data in nonexperimental studies.

2 Clearly, P ( Y = y | do ( X = x )) is equivalent to P ( Yx = y ). This is what we normally assess in a controlled experiment, with X randomized, in which the distribution of Y is estimated for each level x of X .

3 Linear relations are used here for illustration purposes only; they do not represent typical disease-symptom relations but illustrate the historical development of path analysis. Additionally, we will use standardized variables, that is, zero mean and unit variance.

4 Additional implications called “dormant independence” ( Shpitser and Pearl, 2008 ) may be deduced from some graphs with correlated errors ( Verma and Pearl, 1990 ).

5 A simple proof of the Causal Markov Theorem is given in Pearl (2000a , p. 30). This theorem was first presented in Pearl and Verma (1991) , but it is implicit in the works of Kiiveri, Speed, and Carlin (1984) and others. Corollary 1 was named “Manipulation Theorem” in Spirtes et al. (1993) , and is also implicit in Robins’ (1987) G -computation formula. See Lauritzen (2001) .

6 For clarity, we drop the (superfluous) subscript 0 from x 0 and z 2 0 .

7 Before applying this criterion, one may delete from the causal graph all nodes that are not ancestors of Y .

8 The reason for this fundamental limitation is that no death case can be tested twice, with and without treatment. For example, if we measure equal proportions of deaths in the treatment and control groups, we cannot tell how many death cases are actually attributable to the treatment itself; it is quite possible that many of those who died under treatment would be alive if untreated and, simultaneously, many of those who survived with treatment would have died if not treated.

9 Connections between structural equations and a restricted class of counterfactuals were first recognized by Simon and Rescher (1966) . These were later generalized by Balke and Pearl (1995) , using surgeries ( Eq. (29) ), thus permitting endogenous variables to serve as counterfactual antecedents. The term “surgery definition” was used in Pearl (2000a , Epilogue) and criticized by Cartwright (2007) and Heckman (2005) , (see Pearl (2009b , pp. 362–3, 374–9 for rebuttals)).

10 The distinction between general, or population-level causes (e.g., “Drinking hemlock causes death”) and singular or unit-level causes (e.g., “Socrates’ drinking hemlock caused his death”), which many philosophers have regarded as irreconcilable ( Eells, 1991 ), introduces no tension at all in the structural theory. The two types of sentences differ merely in the level of situation-specific information that is brought to bear on a problem, that is, in the specificity of the evidence e that enters the quantity P ( Y x = y | e ). When e includes all factors u , we have a deterministic, unit-level causation on our hand; when e contains only a few known attributes (e.g., age, income, occupation etc.) while others are assigned probabilities, a population-level analysis ensues.

11 For example, “The probability is 80% that Joe belongs to the class of patients who will be cured if they take the drug and die otherwise.”

12 Note that β in Eq. (1) , the incremental causal effect of X on Y , is defined procedurally by β ≜ E ( Y | d o ( x 0 + 1 ) ) − E ( Y | d o ( x 0 ) ) = ∂ ∂ x E ( Y | d o ( x ) ) = ∂ ∂ x E ( Y x ) . Naturally, all attempts to give β statistical interpretation have ended in frustrations ( Holland, 1988 , Whittaker, 1990 , Wermuth, 1992 , Wermuth and Cox, 1993 ), some persisting well into the 21st century ( Sobel, 2008 ).

13 These equivalence classes were later called “principal stratification” by Frangakis and Rubin (2002) . Looser bounds were derived earlier by Robins (1989) and Manski (1990) .

14 The notation Y ⊥⊥ X | Z stands for the conditional independence relationship P ( Y = y , X = x | Z = z ) = P ( Y = y | Z = z ) P ( X = x | Z = z ) ( Dawid, 1979 ).

15 Inquisitive readers are invited to guess whether X z ⊥⊥ Z | Y holds in Fig. 2(a) , then reflect on why causality is so slow in penetrating statistical education.

16 The opaqueness of counterfactual independencies explains why many researchers within the potential-outcome camp are unaware of the fact that adding a covariate to the analysis (e.g., Z 3 in Fig. 4 , Z in Fig. 5 may actually increase confounding bias in propensity-score matching. Paul Rosenbaum, for example, writes: “there is little or no reason to avoid adjustment for a true covariate, a variable describing subjects before treatment” ( Rosenbaum, 2002 , p. 76). Rubin (2009) goes as far as stating that refraining from conditioning on an available measurement is “nonscientific ad hockery” for it goes against the tenets of Bayesian philosophy (see ( Pearl, 2009c , d , Heckman and Navarro-Lozano, 2004 ) for a discussion of this fallacy).

17 Such symbiosis is now standard in epidemiology research ( Robins, 2001 , Petersen, Sinisi, and van der Laan, 2006 , VanderWeele and Robins, 2007 , Hafeman and Schwartz, 2009 , VanderWeele, 2009 ) yet still lacking in econometrics ( Heckman, 2008 , Imbens and Wooldridge, 2009 ).

18 All articles cited above define the direct and indirect effects through their regressional interpretations; I am not aware of any article in this tradition that formally adapts a causal interpretation, free of estimation-specific parameterization.

19 Such symbiosis is now standard in epidemiology research ( Robins, 2001 , Petersen et al., 2006 , VanderWeele and Robins, 2007 , Hafeman and Schwartz, 2009 , VanderWeele, 2009 ) and is making its way slowly toward the social and behavioral sciences.

* Portions of this paper are adapted from Pearl (2000a , 2009a , b) ; I am indebted to Elja Arjas, Sander Greenland, David MacKinnon, Patrick Shrout, and many readers of the UCLA Causality Blog ( http://www.mii.ucla.edu/causality/ ) for reading and commenting on various segments of this manuscript, and especially to Erica Moodie and David Stephens for their thorough editorial input. This research was supported in parts by NIH grant #1R01 LM009961-01, NSF grant #IIS-0914211, and ONR grant #N000-14-09-1-0665.

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Causal Research (Explanatory research)

Causal research, also known as explanatory research is conducted in order to identify the extent and nature of cause-and-effect relationships. Causal research can be conducted in order to assess impacts of specific changes on existing norms, various processes etc.

Causal studies focus on an analysis of a situation or a specific problem to explain the patterns of relationships between variables. Experiments  are the most popular primary data collection methods in studies with causal research design.

The presence of cause cause-and-effect relationships can be confirmed only if specific causal evidence exists. Causal evidence has three important components:

1. Temporal sequence . The cause must occur before the effect. For example, it would not be appropriate to credit the increase in sales to rebranding efforts if the increase had started before the rebranding.

2. Concomitant variation . The variation must be systematic between the two variables. For example, if a company doesn’t change its employee training and development practices, then changes in customer satisfaction cannot be caused by employee training and development.

3. Nonspurious association . Any covarioaton between a cause and an effect must be true and not simply due to other variable. In other words, there should be no a ‘third’ factor that relates to both, cause, as well as, effect.

The table below compares the main characteristics of causal research to exploratory and descriptive research designs: [1]

Main characteristics of research designs

 Examples of Causal Research (Explanatory Research)

The following are examples of research objectives for causal research design:

• To assess the impacts of foreign direct investment on the levels of economic growth in Taiwan
• To analyse the effects of re-branding initiatives on the levels of customer loyalty
• To identify the nature of impact of work process re-engineering on the levels of employee motivation

Advantages of Causal Research (Explanatory Research)

• Causal studies may play an instrumental role in terms of identifying reasons behind a wide range of processes, as well as, assessing the impacts of changes on existing norms, processes etc.
• Causal studies usually offer the advantages of replication if necessity arises
• This type of studies are associated with greater levels of internal validity due to systematic selection of subjects

Disadvantages of Causal Research (Explanatory Research)

• Coincidences in events may be perceived as cause-and-effect relationships. For example, Punxatawney Phil was able to forecast the duration of winter for five consecutive years, nevertheless, it is just a rodent without intellect and forecasting powers, i.e. it was a coincidence.
• It can be difficult to reach appropriate conclusions on the basis of causal research findings. This is due to the impact of a wide range of factors and variables in social environment. In other words, while casualty can be inferred, it cannot be proved with a high level of certainty.
• It certain cases, while correlation between two variables can be effectively established; identifying which variable is a cause and which one is the impact can be a difficult task to accomplish.

My e-book,  The Ultimate Guide to Writing a Dissertation in Business Studies: a step by step assistance  contains discussions of theory and application of research designs. The e-book also explains all stages of the  research process  starting from the  selection of the research area  to writing personal reflection. Important elements of dissertations such as  research philosophy ,  research approach ,  methods of data collection ,  data analysis  and  sampling  are explained in this e-book in simple words.

John Dudovskiy

[1] Source: Zikmund, W.G., Babin, J., Carr, J. & Griffin, M. (2012) “Business Research Methods: with Qualtrics Printed Access Card” Cengage Learning

Causal Research: Definition, Design, Tips, Examples

Appinio Research · 21.02.2024 · 33min read

Ever wondered why certain events lead to specific outcomes? Understanding causality—the relationship between cause and effect—is crucial for unraveling the mysteries of the world around us. In this guide on causal research, we delve into the methods, techniques, and principles behind identifying and establishing cause-and-effect relationships between variables. Whether you're a seasoned researcher or new to the field, this guide will equip you with the knowledge and tools to conduct rigorous causal research and draw meaningful conclusions that can inform decision-making and drive positive change.

What is Causal Research?

Causal research is a methodological approach used in scientific inquiry to investigate cause-and-effect relationships between variables. Unlike correlational or descriptive research, which merely examine associations or describe phenomena, causal research aims to determine whether changes in one variable cause changes in another variable.

Importance of Causal Research

Understanding the importance of causal research is crucial for appreciating its role in advancing knowledge and informing decision-making across various fields. Here are key reasons why causal research is significant:

• Establishing Causality:  Causal research enables researchers to determine whether changes in one variable directly cause changes in another variable. This helps identify effective interventions, predict outcomes, and inform evidence-based practices.
• Guiding Policy and Practice:  By identifying causal relationships, causal research provides empirical evidence to support policy decisions, program interventions, and business strategies. Decision-makers can use causal findings to allocate resources effectively and address societal challenges.
• Informing Predictive Modeling:  Causal research contributes to the development of predictive models by elucidating causal mechanisms underlying observed phenomena. Predictive models based on causal relationships can accurately forecast future outcomes and trends.
• Advancing Scientific Knowledge:  Causal research contributes to the cumulative body of scientific knowledge by testing hypotheses, refining theories, and uncovering underlying mechanisms of phenomena. It fosters a deeper understanding of complex systems and phenomena.
• Mitigating Confounding Factors:  Understanding causal relationships allows researchers to control for confounding variables and reduce bias in their studies. By isolating the effects of specific variables, researchers can draw more valid and reliable conclusions.

Causal Research Distinction from Other Research

Understanding the distinctions between causal research and other types of research methodologies is essential for researchers to choose the most appropriate approach for their study objectives. Let's explore the differences and similarities between causal research and descriptive, exploratory, and correlational research methodologies .

Descriptive vs. Causal Research

Descriptive research  focuses on describing characteristics, behaviors, or phenomena without manipulating variables or establishing causal relationships. It provides a snapshot of the current state of affairs but does not attempt to explain why certain phenomena occur.

Causal research , on the other hand, seeks to identify cause-and-effect relationships between variables by systematically manipulating independent variables and observing their effects on dependent variables. Unlike descriptive research, causal research aims to determine whether changes in one variable directly cause changes in another variable.

Similarities:

• Both descriptive and causal research involve empirical observation and data collection.
• Both types of research contribute to the scientific understanding of phenomena, albeit through different approaches.

Differences:

• Descriptive research focuses on describing phenomena, while causal research aims to explain why phenomena occur by identifying causal relationships.
• Descriptive research typically uses observational methods, while causal research often involves experimental designs or causal inference techniques to establish causality.

Exploratory vs. Causal Research

Exploratory research  aims to explore new topics, generate hypotheses, or gain initial insights into phenomena. It is often conducted when little is known about a subject and seeks to generate ideas for further investigation.

Causal research , on the other hand, is concerned with testing hypotheses and establishing cause-and-effect relationships between variables. It builds on existing knowledge and seeks to confirm or refute causal hypotheses through systematic investigation.

• Both exploratory and causal research contribute to the generation of knowledge and theory development.
• Both types of research involve systematic inquiry and data analysis to answer research questions.
• Exploratory research focuses on generating hypotheses and exploring new areas of inquiry, while causal research aims to test hypotheses and establish causal relationships.
• Exploratory research is more flexible and open-ended, while causal research follows a more structured and hypothesis-driven approach.

Correlational vs. Causal Research

Correlational research  examines the relationship between variables without implying causation. It identifies patterns of association or co-occurrence between variables but does not establish the direction or causality of the relationship.

Causal research , on the other hand, seeks to establish cause-and-effect relationships between variables by systematically manipulating independent variables and observing their effects on dependent variables. It goes beyond mere association to determine whether changes in one variable directly cause changes in another variable.

• Both correlational and causal research involve analyzing relationships between variables.
• Both types of research contribute to understanding the nature of associations between variables.
• Correlational research focuses on identifying patterns of association, while causal research aims to establish causal relationships.
• Correlational research does not manipulate variables, while causal research involves systematically manipulating independent variables to observe their effects on dependent variables.

How to Formulate Causal Research Hypotheses?

Crafting research questions and hypotheses is the foundational step in any research endeavor. Defining your variables clearly and articulating the causal relationship you aim to investigate is essential. Let's explore this process further.

1. Identify Variables

Identifying variables involves recognizing the key factors you will manipulate or measure in your study. These variables can be classified into independent, dependent, and confounding variables.

• Independent Variable (IV):  This is the variable you manipulate or control in your study. It is the presumed cause that you want to test.
• Dependent Variable (DV):  The dependent variable is the outcome or response you measure. It is affected by changes in the independent variable.
• Confounding Variables:  These are extraneous factors that may influence the relationship between the independent and dependent variables, leading to spurious correlations or erroneous causal inferences. Identifying and controlling for confounding variables is crucial for establishing valid causal relationships.

2. Establish Causality

Establishing causality requires meeting specific criteria outlined by scientific methodology. While correlation between variables may suggest a relationship, it does not imply causation. To establish causality, researchers must demonstrate the following:

• Temporal Precedence:  The cause must precede the effect in time. In other words, changes in the independent variable must occur before changes in the dependent variable.
• Covariation of Cause and Effect:  Changes in the independent variable should be accompanied by corresponding changes in the dependent variable. This demonstrates a consistent pattern of association between the two variables.
• Elimination of Alternative Explanations:  Researchers must rule out other possible explanations for the observed relationship between variables. This involves controlling for confounding variables and conducting rigorous experimental designs to isolate the effects of the independent variable.

3. Write Clear and Testable Hypotheses

Hypotheses serve as tentative explanations for the relationship between variables and provide a framework for empirical testing. A well-formulated hypothesis should be:

• Specific:  Clearly state the expected relationship between the independent and dependent variables.
• Testable:  The hypothesis should be capable of being empirically tested through observation or experimentation.
• Falsifiable:  There should be a possibility of proving the hypothesis false through empirical evidence.

For example, a hypothesis in a study examining the effect of exercise on weight loss could be: "Increasing levels of physical activity (IV) will lead to greater weight loss (DV) among participants (compared to those with lower levels of physical activity)."

By formulating clear hypotheses and operationalizing variables, researchers can systematically investigate causal relationships and contribute to the advancement of scientific knowledge.

Causal Research Design

Designing your research study involves making critical decisions about how you will collect and analyze data to investigate causal relationships.

Experimental vs. Observational Designs

One of the first decisions you'll make when designing a study is whether to employ an experimental or observational design. Each approach has its strengths and limitations, and the choice depends on factors such as the research question, feasibility , and ethical considerations.

• Experimental Design: In experimental designs, researchers manipulate the independent variable and observe its effects on the dependent variable while controlling for confounding variables. Random assignment to experimental conditions allows for causal inferences to be drawn. Example: A study testing the effectiveness of a new teaching method on student performance by randomly assigning students to either the experimental group (receiving the new teaching method) or the control group (receiving the traditional method).
• Observational Design: Observational designs involve observing and measuring variables without intervention. Researchers may still examine relationships between variables but cannot establish causality as definitively as in experimental designs. Example: A study observing the association between socioeconomic status and health outcomes by collecting data on income, education level, and health indicators from a sample of participants.

Control and Randomization

Control and randomization are crucial aspects of experimental design that help ensure the validity of causal inferences.

• Control: Controlling for extraneous variables involves holding constant factors that could influence the dependent variable, except for the independent variable under investigation. This helps isolate the effects of the independent variable. Example: In a medication trial, controlling for factors such as age, gender, and pre-existing health conditions ensures that any observed differences in outcomes can be attributed to the medication rather than other variables.
• Randomization: Random assignment of participants to experimental conditions helps distribute potential confounders evenly across groups, reducing the likelihood of systematic biases and allowing for causal conclusions. Example: Randomly assigning patients to treatment and control groups in a clinical trial ensures that both groups are comparable in terms of baseline characteristics, minimizing the influence of extraneous variables on treatment outcomes.

Internal and External Validity

Two key concepts in research design are internal validity and external validity, which relate to the credibility and generalizability of study findings, respectively.

• Internal Validity: Internal validity refers to the extent to which the observed effects can be attributed to the manipulation of the independent variable rather than confounding factors. Experimental designs typically have higher internal validity due to their control over extraneous variables. Example: A study examining the impact of a training program on employee productivity would have high internal validity if it could confidently attribute changes in productivity to the training intervention.
• External Validity: External validity concerns the extent to which study findings can be generalized to other populations, settings, or contexts. While experimental designs prioritize internal validity, they may sacrifice external validity by using highly controlled conditions that do not reflect real-world scenarios. Example: Findings from a laboratory study on memory retention may have limited external validity if the experimental tasks and conditions differ significantly from real-life learning environments.

Types of Experimental Designs

Several types of experimental designs are commonly used in causal research, each with its own strengths and applications.

• Randomized Control Trials (RCTs): RCTs are considered the gold standard for assessing causality in research. Participants are randomly assigned to experimental and control groups, allowing researchers to make causal inferences. Example: A pharmaceutical company testing a new drug's efficacy would use an RCT to compare outcomes between participants receiving the drug and those receiving a placebo.
• Quasi-Experimental Designs: Quasi-experimental designs lack random assignment but still attempt to establish causality by controlling for confounding variables through design or statistical analysis . Example: A study evaluating the effectiveness of a smoking cessation program might compare outcomes between participants who voluntarily enroll in the program and a matched control group of non-enrollees.

By carefully selecting an appropriate research design and addressing considerations such as control, randomization, and validity, researchers can conduct studies that yield credible evidence of causal relationships and contribute valuable insights to their field of inquiry.

Causal Research Data Collection

Collecting data is a critical step in any research study, and the quality of the data directly impacts the validity and reliability of your findings.

Choosing Measurement Instruments

Selecting appropriate measurement instruments is essential for accurately capturing the variables of interest in your study. The choice of measurement instrument depends on factors such as the nature of the variables, the target population , and the research objectives.

• Surveys :  Surveys are commonly used to collect self-reported data on attitudes, opinions, behaviors, and demographics . They can be administered through various methods, including paper-and-pencil surveys, online surveys, and telephone interviews.
• Observations:  Observational methods involve systematically recording behaviors, events, or phenomena as they occur in natural settings. Observations can be structured (following a predetermined checklist) or unstructured (allowing for flexible data collection).
• Psychological Tests:  Psychological tests are standardized instruments designed to measure specific psychological constructs, such as intelligence, personality traits, or emotional functioning. These tests often have established reliability and validity.
• Physiological Measures:  Physiological measures, such as heart rate, blood pressure, or brain activity, provide objective data on bodily processes. They are commonly used in health-related research but require specialized equipment and expertise.
• Existing Databases:  Researchers may also utilize existing datasets, such as government surveys, public health records, or organizational databases, to answer research questions. Secondary data analysis can be cost-effective and time-saving but may be limited by the availability and quality of data.

Ensuring accurate data collection is the cornerstone of any successful research endeavor. With the right tools in place, you can unlock invaluable insights to drive your causal research forward. From surveys to tests, each instrument offers a unique lens through which to explore your variables of interest.

At Appinio , we understand the importance of robust data collection methods in informing impactful decisions. Let us empower your research journey with our intuitive platform, where you can effortlessly gather real-time consumer insights to fuel your next breakthrough.   Ready to take your research to the next level? Book a demo today and see how Appinio can revolutionize your approach to data collection!

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Sampling Techniques

Sampling involves selecting a subset of individuals or units from a larger population to participate in the study. The goal of sampling is to obtain a representative sample that accurately reflects the characteristics of the population of interest.

• Probability Sampling:  Probability sampling methods involve randomly selecting participants from the population, ensuring that each member of the population has an equal chance of being included in the sample. Common probability sampling techniques include simple random sampling , stratified sampling, and cluster sampling .
• Non-Probability Sampling:  Non-probability sampling methods do not involve random selection and may introduce biases into the sample. Examples of non-probability sampling techniques include convenience sampling, purposive sampling, and snowball sampling.

The choice of sampling technique depends on factors such as the research objectives, population characteristics, resources available, and practical constraints. Researchers should strive to minimize sampling bias and maximize the representativeness of the sample to enhance the generalizability of their findings.

Ethical Considerations

Ethical considerations are paramount in research and involve ensuring the rights, dignity, and well-being of research participants. Researchers must adhere to ethical principles and guidelines established by professional associations and institutional review boards (IRBs).

• Informed Consent:  Participants should be fully informed about the nature and purpose of the study, potential risks and benefits, their rights as participants, and any confidentiality measures in place. Informed consent should be obtained voluntarily and without coercion.
• Privacy and Confidentiality:  Researchers should take steps to protect the privacy and confidentiality of participants' personal information. This may involve anonymizing data, securing data storage, and limiting access to identifiable information.
• Minimizing Harm:  Researchers should mitigate any potential physical, psychological, or social harm to participants. This may involve conducting risk assessments, providing appropriate support services, and debriefing participants after the study.
• Respect for Participants:  Researchers should respect participants' autonomy, diversity, and cultural values. They should seek to foster a trusting and respectful relationship with participants throughout the research process.
• Publication and Dissemination:  Researchers have a responsibility to accurately report their findings and acknowledge contributions from participants and collaborators. They should adhere to principles of academic integrity and transparency in disseminating research results.

By addressing ethical considerations in research design and conduct, researchers can uphold the integrity of their work, maintain trust with participants and the broader community, and contribute to the responsible advancement of knowledge in their field.

Causal Research Data Analysis

Once data is collected, it must be analyzed to draw meaningful conclusions and assess causal relationships.

Causal Inference Methods

Causal inference methods are statistical techniques used to identify and quantify causal relationships between variables in observational data. While experimental designs provide the most robust evidence for causality, observational studies often require more sophisticated methods to account for confounding factors.

• Difference-in-Differences (DiD):  DiD compares changes in outcomes before and after an intervention between a treatment group and a control group, controlling for pre-existing trends. It estimates the average treatment effect by differencing the changes in outcomes between the two groups over time.
• Instrumental Variables (IV):  IV analysis relies on instrumental variables—variables that affect the treatment variable but not the outcome—to estimate causal effects in the presence of endogeneity. IVs should be correlated with the treatment but uncorrelated with the error term in the outcome equation.
• Regression Discontinuity (RD):  RD designs exploit naturally occurring thresholds or cutoff points to estimate causal effects near the threshold. Participants just above and below the threshold are compared, assuming that they are similar except for their proximity to the threshold.
• Propensity Score Matching (PSM):  PSM matches individuals or units based on their propensity scores—the likelihood of receiving the treatment—creating comparable groups with similar observed characteristics. Matching reduces selection bias and allows for causal inference in observational studies.

Assessing Causality Strength

Assessing the strength of causality involves determining the magnitude and direction of causal effects between variables. While statistical significance indicates whether an observed relationship is unlikely to occur by chance, it does not necessarily imply a strong or meaningful effect.

• Effect Size:  Effect size measures the magnitude of the relationship between variables, providing information about the practical significance of the results. Standard effect size measures include Cohen's d for mean differences and odds ratios for categorical outcomes.
• Confidence Intervals:  Confidence intervals provide a range of values within which the actual effect size is likely to lie with a certain degree of certainty. Narrow confidence intervals indicate greater precision in estimating the true effect size.
• Practical Significance:  Practical significance considers whether the observed effect is meaningful or relevant in real-world terms. Researchers should interpret results in the context of their field and the implications for stakeholders.

Handling Confounding Variables

Confounding variables are extraneous factors that may distort the observed relationship between the independent and dependent variables, leading to spurious or biased conclusions. Addressing confounding variables is essential for establishing valid causal inferences.

• Statistical Control:  Statistical control involves including confounding variables as covariates in regression models to partially out their effects on the outcome variable. Controlling for confounders reduces bias and strengthens the validity of causal inferences.
• Matching:  Matching participants or units based on observed characteristics helps create comparable groups with similar distributions of confounding variables. Matching reduces selection bias and mimics the randomization process in experimental designs.
• Sensitivity Analysis:  Sensitivity analysis assesses the robustness of study findings to changes in model specifications or assumptions. By varying analytical choices and examining their impact on results, researchers can identify potential sources of bias and evaluate the stability of causal estimates.
• Subgroup Analysis:  Subgroup analysis explores whether the relationship between variables differs across subgroups defined by specific characteristics. Identifying effect modifiers helps understand the conditions under which causal effects may vary.

By employing rigorous causal inference methods, assessing the strength of causality, and addressing confounding variables, researchers can confidently draw valid conclusions about causal relationships in their studies, advancing scientific knowledge and informing evidence-based decision-making.

Causal Research Examples

Examples play a crucial role in understanding the application of causal research methods and their impact across various domains. Let's explore some detailed examples to illustrate how causal research is conducted and its real-world implications:

Example 1: Software as a Service (SaaS) User Retention Analysis

Suppose a SaaS company wants to understand the factors influencing user retention and engagement with their platform. The company conducts a longitudinal observational study, collecting data on user interactions, feature usage, and demographic information over several months.

• Design:  The company employs an observational cohort study design, tracking cohorts of users over time to observe changes in retention and engagement metrics. They use analytics tools to collect data on user behavior , such as logins, feature usage, session duration, and customer support interactions.
• Data Collection:  Data is collected from the company's platform logs, customer relationship management (CRM) system, and user surveys. Key metrics include user churn rates, active user counts, feature adoption rates, and Net Promoter Scores ( NPS ).
• Analysis:  Using statistical techniques like survival analysis and regression modeling, the company identifies factors associated with user retention, such as feature usage patterns, onboarding experiences, customer support interactions, and subscription plan types.
• Findings: The analysis reveals that users who engage with specific features early in their lifecycle have higher retention rates, while those who encounter usability issues or lack personalized onboarding experiences are more likely to churn. The company uses these insights to optimize product features, improve onboarding processes, and enhance customer support strategies to increase user retention and satisfaction.

Example 2: Business Impact of Digital Marketing Campaign

Consider a technology startup launching a digital marketing campaign to promote its new product offering. The company conducts an experimental study to evaluate the effectiveness of different marketing channels in driving website traffic, lead generation, and sales conversions.

• Design:  The company implements an A/B testing design, randomly assigning website visitors to different marketing treatment conditions, such as Google Ads, social media ads, email campaigns, or content marketing efforts. They track user interactions and conversion events using web analytics tools and marketing automation platforms.
• Data Collection:  Data is collected on website traffic, click-through rates, conversion rates, lead generation, and sales revenue. The company also gathers demographic information and user feedback through surveys and customer interviews to understand the impact of marketing messages and campaign creatives .
• Analysis:  Utilizing statistical methods like hypothesis testing and multivariate analysis, the company compares key performance metrics across different marketing channels to assess their effectiveness in driving user engagement and conversion outcomes. They calculate return on investment (ROI) metrics to evaluate the cost-effectiveness of each marketing channel.
• Findings:  The analysis reveals that social media ads outperform other marketing channels in generating website traffic and lead conversions, while email campaigns are more effective in nurturing leads and driving sales conversions. Armed with these insights, the company allocates marketing budgets strategically, focusing on channels that yield the highest ROI and adjusting messaging and targeting strategies to optimize campaign performance.

These examples demonstrate the diverse applications of causal research methods in addressing important questions, informing policy decisions, and improving outcomes in various fields. By carefully designing studies, collecting relevant data, employing appropriate analysis techniques, and interpreting findings rigorously, researchers can generate valuable insights into causal relationships and contribute to positive social change.

How to Interpret Causal Research Results?

Interpreting and reporting research findings is a crucial step in the scientific process, ensuring that results are accurately communicated and understood by stakeholders.

Interpreting Statistical Significance

Statistical significance indicates whether the observed results are unlikely to occur by chance alone, but it does not necessarily imply practical or substantive importance. Interpreting statistical significance involves understanding the meaning of p-values and confidence intervals and considering their implications for the research findings.

• P-values:  A p-value represents the probability of obtaining the observed results (or more extreme results) if the null hypothesis is true. A p-value below a predetermined threshold (typically 0.05) suggests that the observed results are statistically significant, indicating that the null hypothesis can be rejected in favor of the alternative hypothesis.
• Confidence Intervals:  Confidence intervals provide a range of values within which the true population parameter is likely to lie with a certain degree of confidence (e.g., 95%). If the confidence interval does not include the null value, it suggests that the observed effect is statistically significant at the specified confidence level.

Interpreting statistical significance requires considering factors such as sample size, effect size, and the practical relevance of the results rather than relying solely on p-values to draw conclusions.

Discussing Practical Significance

While statistical significance indicates whether an effect exists, practical significance evaluates the magnitude and meaningfulness of the effect in real-world terms. Discussing practical significance involves considering the relevance of the results to stakeholders and assessing their impact on decision-making and practice.

• Effect Size:  Effect size measures the magnitude of the observed effect, providing information about its practical importance. Researchers should interpret effect sizes in the context of their field and the scale of measurement (e.g., small, medium, or large effect sizes).
• Contextual Relevance:  Consider the implications of the results for stakeholders, policymakers, and practitioners. Are the observed effects meaningful in the context of existing knowledge, theory, or practical applications? How do the findings contribute to addressing real-world problems or informing decision-making?

Discussing practical significance helps contextualize research findings and guide their interpretation and application in practice, beyond statistical significance alone.

Addressing Limitations and Assumptions

No study is without limitations, and researchers should transparently acknowledge and address potential biases, constraints, and uncertainties in their research design and findings.

• Methodological Limitations:  Identify any limitations in study design, data collection, or analysis that may affect the validity or generalizability of the results. For example, sampling biases , measurement errors, or confounding variables.
• Assumptions:  Discuss any assumptions made in the research process and their implications for the interpretation of results. Assumptions may relate to statistical models, causal inference methods, or theoretical frameworks underlying the study.
• Alternative Explanations:  Consider alternative explanations for the observed results and discuss their potential impact on the validity of causal inferences. How robust are the findings to different interpretations or competing hypotheses?

Addressing limitations and assumptions demonstrates transparency and rigor in the research process, allowing readers to critically evaluate the validity and reliability of the findings.

Communicating Findings Clearly

Effectively communicating research findings is essential for disseminating knowledge, informing decision-making, and fostering collaboration and dialogue within the scientific community.

• Clarity and Accessibility:  Present findings in a clear, concise, and accessible manner, using plain language and avoiding jargon or technical terminology. Organize information logically and use visual aids (e.g., tables, charts, graphs) to enhance understanding.
• Contextualization:  Provide context for the results by summarizing key findings, highlighting their significance, and relating them to existing literature or theoretical frameworks. Discuss the implications of the findings for theory, practice, and future research directions.
• Transparency:  Be transparent about the research process, including data collection procedures, analytical methods, and any limitations or uncertainties associated with the findings. Clearly state any conflicts of interest or funding sources that may influence interpretation.

By communicating findings clearly and transparently, researchers can facilitate knowledge exchange, foster trust and credibility, and contribute to evidence-based decision-making.

Causal Research Tips

When conducting causal research, it's essential to approach your study with careful planning, attention to detail, and methodological rigor. Here are some tips to help you navigate the complexities of causal research effectively:

• Define Clear Research Questions:  Start by clearly defining your research questions and hypotheses. Articulate the causal relationship you aim to investigate and identify the variables involved.
• Consider Alternative Explanations:  Be mindful of potential confounding variables and alternative explanations for the observed relationships. Take steps to control for confounders and address alternative hypotheses in your analysis.
• Prioritize Internal Validity:  While external validity is important for generalizability, prioritize internal validity in your study design to ensure that observed effects can be attributed to the manipulation of the independent variable.
• Use Randomization When Possible:  If feasible, employ randomization in experimental designs to distribute potential confounders evenly across experimental conditions and enhance the validity of causal inferences.
• Be Transparent About Methods:  Provide detailed descriptions of your research methods, including data collection procedures, analytical techniques, and any assumptions or limitations associated with your study.
• Utilize Multiple Methods:  Consider using a combination of experimental and observational methods to triangulate findings and strengthen the validity of causal inferences.
• Be Mindful of Sample Size:  Ensure that your sample size is adequate to detect meaningful effects and minimize the risk of Type I and Type II errors. Conduct power analyses to determine the sample size needed to achieve sufficient statistical power.
• Validate Measurement Instruments:  Validate your measurement instruments to ensure that they are reliable and valid for assessing the variables of interest in your study. Pilot test your instruments if necessary.
• Seek Feedback from Peers:  Collaborate with colleagues or seek feedback from peer reviewers to solicit constructive criticism and improve the quality of your research design and analysis.

Conclusion for Causal Research

Mastering causal research empowers researchers to unlock the secrets of cause and effect, shedding light on the intricate relationships between variables in diverse fields. By employing rigorous methods such as experimental designs, causal inference techniques, and careful data analysis, you can uncover causal mechanisms, predict outcomes, and inform evidence-based practices. Through the lens of causal research, complex phenomena become more understandable, and interventions become more effective in addressing societal challenges and driving progress. In a world where understanding the reasons behind events is paramount, causal research serves as a beacon of clarity and insight. Armed with the knowledge and techniques outlined in this guide, you can navigate the complexities of causality with confidence, advancing scientific knowledge, guiding policy decisions, and ultimately making meaningful contributions to our understanding of the world.

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29 Causation and Explanation

Peter Lipton passed away on 25 November 2007, as this volume was being prepared. He was the author of Inference to the Best Explanation (Routledge, 1991) and numerous articles in the philosophy of science. He was Head of Cambridge University's Department of History and Philosophy of Science for many years. He earned a reputation as a gifted teacher and caring mentor. He will be sorely missed by family and friends, students and colleagues, and the profession of philosophy.

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In its simplest form, a causal model of explanation maintains that to explain some phenomenon is to give some information about its causes. This prompts four questions that will structure the discussion to follow. The first is whether all explanations are causal. The second is whether all causes are explanatory. The answer to both of these questions turns out to be negative, and seeing why this is so helps to clarify the relationship between causation and explanation. The third question is itself a request for an explanation: Why do causes explain, when they do? Why, for example, do causes explain their effects but effects not explain their causes? Finally, the article considers how explanation can illuminate the process of causal inference.

1. Introduction

There are intimate connections between causation and explanation, between cause and because, and this suggests the projects of illuminating one in terms of the other. Aristotle, for example, appears to have understood his notion of efficient causation in terms of explanation (Sorabji 1980 ). Nowadays it is not so common to attempt to use explanation to analyse the metaphysics of causation, though there is considerable interest in using explanation to analyse the epistemology of causation, to see explanatory considerations as a guide to causal inference (Lipton 2004 ). On the metaphysical level, the analysis has more commonly gone in the other direction, to causal theories of explanation rather than explanatory theories of causation (Salmon 1984 ; Lewis 1986 ; Woodward 2003 ). As readers of this Handbook will be aware, the nature of causation is itself highly contested, but the absence of an agreed account has not stopped philosophers from helping themselves to the notion of causation to account for other things, and philosophers of explanation are no exception. The practice is benign and potentially illuminating, so long as one does not go on to attempt to analyse causation in terms of explanation and so create a circle.

In its simplest form, a causal model of explanation maintains that to explain some phenomenon is to give some information about its causes. This prompts four questions that will structure the discussion to follow. The first is whether all explanations are causal. The second is whether all causes are explanatory. The answer to both of these questions turns out to be negative, and seeing why this is so helps to clarify the relationship between causation and explanation. The third question is itself a request for an explanation: Why do causes explain, when they do? Why, for example, do causes explain their effects but effects not explain their causes? Finally, we will consider how explanation can illuminate the process of causal inference.

2. Are All Explanations Causal?

The causal model of explanation has considerable attractions. Both science and ordinary life are filled with causal explanations, and the causes we cite seem explanatory precisely because they are causes. Indeed it appears that requests for explanation, why‐questions, can often be paraphrased as what‐is‐the‐cause‐of questions. Moreover, the causal model passes three key tests for any adequate account of explanation, tests that other popular models of explanation fail. The first of these is that a model should account for the difference between knowing and understanding. Knowing that something is the case is necessary but not sufficient for understanding why it is the case. We all know that the sky is sometimes blue, but few of us understand why. Typically, when people ask questions of the form ‘Why P ?’, they already know that P , so understanding why must require something more than knowing that. The causal model gives a natural account of this gap, since we can know that something occurred without knowing what caused it to occur. (By contrast, a model according to which we understand why something occurs by seeing that it was to be expected (Hempel 1965 : 337, 364–76) seems not to pass this test, since simply knowing that P will often already involve having good reasons to believe that P and indeed good reasons to expect P .)

The second test is the test of the why‐regress. As most of us discovered in our youth and to our parents’ consternation, whatever answer someone gives to a why‐question, it is almost always possible sensibly to ask why the explanation itself is so. Thus there is a potential regress of explanations. If your daughter asks you why the same side of the moon always faces the earth, you may reply that this is because the period of the moon's orbit around the earth is the same as the period of the moon's spin about its own axis. This may be a good explanation, but it does not preclude your daughter from going on to ask the different but excellent question as to why these periods should be the same. For our purposes, the salient feature of the why‐regress is that it is benign: the answer to one why‐question may be explanatory and provide understanding even if we have no answer to why‐questions further up the ladder. This shows that understanding is not like some substance that gets transmitted from explanation to what is explained, since the explanation can bring us to understand why what is explained is so even though we do not also understand why the explanation itself is so. Any account of understanding that would require that we can only use explanations that have themselves been explained fails the test of the why‐regress. The causal model passes this test, because it is possible to know that C caused E without also knowing what caused C . The model thus shows why the why‐regress is benign. (By contrast, a model according to which we explain a phenomenon by reducing it to something familiar (cf. Friedman 1974 : 9–11) may not account so well for the why‐regress, since if the familiarity model were correct, then the explanation would presumably not itself support a why‐question, since it is already familiar. But almost all explanations do support a further why‐question.)

The third test is the test of self‐evidencing explanations (cf. Hempel 1965 : 370–4). These are explanations where what is explained provides an essential part of the reason for believing that the explanation itself is correct. Self‐evidencing explanations are common, in part because we often infer that a hypothesis is correct precisely because it would, if correct, provide a good explanation of the evidence. Seeing the disembowelled teddy bear on the floor, with its stuffing strewn across the living room, I infer that Rex has misbehaved again. Rex's actions provide an excellent if discouraging explanation of the scene before me, and this is so even though that scene is my only direct evidence that the misbehaviour took place. To take a more scientific and less destructive example, the velocity of recession of a galaxy explains the red shift of its characteristic spectrum, even if the observation of that shift is an essential part of the scientist's evidence that the galaxy is indeed receding at the specified velocity. Self‐evidencing explanations exhibit a kind of circularity: H explains E while E is evidence for H . As with the why‐regress, however, what is salient is that there is nothing vicious here: self‐evidencing explanations may be illuminating and well supported. Any account of understanding that rules them out is incorrect. The causal model passes this test too. It allows for self‐evidencing explanations, because it is possible for C to be a cause of E where knowledge of E is an essential part of one's reason for believing that C is indeed a cause. (By contrast, a rational expectation model seems to fail this test too, since if A explains B by giving a reason to believe B , then to suppose that B simultaneously gives a reason to believe A would be to move in a vicious circle; at least it cannot be that A is my reason for B and B is my reason for A .)

Alongside all these virtues, however, the causal model of explanation has an obvious limitation, because not all explanations are causal. Mathematicians and philosophers, for example, give explanations, but mathematical explanations are never causal, and philosophical explanations seldom are. A mathematician may explain why Gödel's Theorem is true, and a philosopher may explain why there can be no inductive justification of induction, but these are not explanations that cite causes. There are even physical explanations that seem non‐causal. Here are two striking examples. First, suppose that a bunch of sticks is thrown into the air with a lot of spin, so that the sticks separate and tumble as they fall. Now freeze the scene at a moment during the sticks’ descent. Why are appreciably more of them near the horizontal axis than near the vertical, rather than in more or less equal numbers near each orientation one might have expected? The answer, roughly speaking, is that there are many more ways for a stick to be near the horizontal than near the vertical. To see this, consider purely horizontal and vertical orientations for a single stick with a fixed midpoint. There are indefinitely many horizontal orientations, but only two vertical orientations. Or think of the shell that the ends of that stick trace as it takes every possible orientation. The areas that correspond to near the vertical are caps centred on the north and south poles formed when the stick is 45° or less off the vertical, and this area is substantially less than half the surface area of the entire sphere. Another way of putting it is that the explanation why more sticks are near the vertical than near the horizontal is that there are two horizontal dimensions but only one vertical one. This is a lovely explanation, but apparently not a causal explanation, since geometrical facts cannot be causes.

The second example of a non‐causal explanation concerns reward and punishment (Kahneman, Slovic, and Tversky 1982 : 66–8). Air Force flight instructors had a policy of strongly praising trainee pilots after an unusually good performance and strongly criticizing them after an unusually weak performance. What they found is that trainees tended to improve after a poor performance and criticism; but they actually tended to do worse after good performance and praise. What explains this pattern? Perhaps it is that criticism is much more effective that praise. That would be a causal explanation. But the pattern of performance is also what one should expect if neither praise nor criticism had any effect. It may just be regression to the mean: extreme performances tend to be followed by less extreme performances. If this is what is going on, we can explain the observed pattern by appeal to chance rather than to any cause. (This example ought to give pause to parents who are too quick to infer that punishing children for bad behaviour is more effective than rewarding them for good behaviour.)

The existence of non‐causal explanations shows that a causal model of explanation cannot be complete. One reaction to this would be to attempt to expand the notion of causation to some broader notion of ‘determination’ that would encompass the non‐causal cases (Ruben 1990 : 230–3). This approach has merit, but it will be difficult to come up with a such a notion that we understand even as well as we understand causation, without falling into the relation of deductive determination, which will expose the model to many of the objections to the deductive‐nomological model, according to which an explanation is a valid argument whose conclusion is a description of the phenomenon to be explained and whose premisses include essentially at least one law (Hempel 1965 : ch. 10). That model faces diverse counterexamples of deductions that are not explanatory, such as the deduction of a law from the conjunction of itself and an unrelated law, or the deduction of a cause from one of its effects plus a law linking the two, such as the deduction of a galaxy's speed of recession from the red shift of its characteristic spectrum (cf. Psillos 2002 : ch. 8). The red shift may entail the recession, but it is the recession that explains the red shift, not conversely. Causes are not the only things that are explanatory, but what makes them explanatory is not that they entail their effects. Indeed one of the signal strengths of the causal model of explanation is that it avoids so many of the weaknesses of the deductive‐nomological model. It is however a weaknesses of the causal model that not all explanations fall within its purview.

3. Are All Causes Explanatory?

Each effect has many causes and not all of them explain it. When a student turns up to his tutorial without an essay written, the teacher may accept as at least a potential explanation the story about the computer crashing, but not ‘Well, you know about the Big Bang…’. The Big Bang is part of the causal history of every other event, but does not explain most of them. What then is the difference between explanatory and unexplanatory causes? One might look to the causes themselves. For example, a distinction is sometimes made between causes that are changes and causes that are standing conditions (Mill 1904 : 3. 5. 3): perhaps, the Big Bang notwithstanding, only changes are generally explanatory. Thus we might explain why the match lit by saying that it was because it was struck, not because there was oxygen present. But standing conditions are sometimes explanatory: we might for example explain why a match lit by saying that it was dry. Indeed the presence of oxygen may explain a fire, for example if the fire takes place in a laboratory environment that was designed to be oxygen‐free (Hart and Honoré 1985 : 35).

One of the reasons we cannot distinguish between explanatory and unexplanatory causes in this way is because the distinction between changes and standing conditions is intrinsic to the cause, whereas the distinction between explanatory and unexplanatory causes is relative to the effect to be explained. The very same cause may explain one effect but not another. For example, the short circuit might explain the fire, but not why the insurance company refused to pay out. So we are better off looking for a demarcation that focuses on the relation between cause and effect. For example, overdetermined causes are often for that reason often not very explanatory. Thus if house is destroyed in an avalanche, mentioning the avalanche explains this better than mentioning only the particular rocks that happen to have hit the house, since if those rocks hadn't hit the house, others would have. But many causes that are not overdetermined are still not explanatory, so this cannot be the whole story.

We can make some progress on the distinction between explanatory and unexplanatory causes by noting that what counts as an explanatory cause depends not only on the effect, but also on our interests. One natural way to account for the way interests help us to select explanations from among causes is to reveal additional structure in the why‐question about the phenomenon to be explained, structure that varies with interest and that points to particular causes. The interest relativity of explanation can be accounted for in part with a contrastive analysis of what is explained. What is explained is not simply ‘Why this?’, but ‘Why this rather than that?’ (van Fraassen 1980 : 126–9; Garfinkel 1981 : 28–41; Lipton 2004 : 30–54). A contrastive phenomenon consists of a fact and a foil, and the same fact may have several different foils. We may not explain why the leaves turn yellow in November simpliciter , but only for example why they turn yellow in November rather than in January, or why they turn yellow in November rather than turn blue.

Why‐questions are often posed explicitly in contrastive form and it is not difficult to come up with examples where different people select different foils, requiring different explanations. Jones's untreated syphilis explains why he rather than Smith (who did not have syphilis) contracted paresis, but not why he rather than Doe (who had syphilis but had it treated) contracted paresis. An explanation of why I went to see Jumpers rather than Candide will probably not explain why I went to see Jumpers rather than staying at home, and an explanation of why Able rather than Baker got the philosophy job may not explain why Able rather that Charles got the job. Since the causes that explain a fact relative to one foil will not generally explain it relative to another, the contrastive question provides a restriction on explanatory causes that goes beyond the identity of the effect.

Although the role of contrasts in why‐questions will not account for all the factors that distinguish explanatory from unexplanatory causes, it goes a considerable way. But how does it work: how does the choice of foil select an explanatory cause? There are various accounts available. Some focus on the ways in which an explanatory cause may probabilistically favour the fact over the foil (van Fraassen 1980 : 146–51; Hitchcock 1999 : 597–608). Others appeal to counterfactuals, requiring of an explanatory cause for example that it would not have been a cause of the foil, had the foil occurred (Lewis 1986 : 229–30). A third kind of account is inspired by a classic principle of causal inference, John Stuart Mill's method of difference, his version of the controlled experiment (Mill 1904 : 3. 8. 2). Mill's method rests on the principle that a cause must lie among the antecedent differences between a case where the effect occurs and an otherwise similar case where it does not. The difference in effect points back to a difference that locates a cause. Thus we might infer that contracting syphilis is a cause of paresis, since it is one of the ways Smith and Jones differed. The cause that the method of difference isolates depends on which control we use. If, instead of Smith, we used Doe, we would be led to say not that a cause of paresis is syphilis, but that it is the failure to treat it.

The method of difference concerns the discovery of causes rather than the explanation of effects, but the similarity to contrastive explanation is striking (Garfinkel 1981 : 40). So there may be an analogous difference condition on contrastive explanation, according to which to explain why P rather than Q , we must cite a causal difference between P and not‐ Q , consisting of a cause of P and the absence of a corresponding event in the case of not‐ Q , where a corresponding event is something that would bear the same relation to Q as the cause of P bears to P (Lipton 2004 : 42–54). On this view, contrastive questions select as explanatory an actual causal difference between P and not‐ Q , consisting of both a presence and an absence. If only Jones had syphilis, that explains why he rather than Smith has paresis, since having syphilis is a condition whose presence was a cause of Jones's paresis and a condition that does not appear in Smith's medical history. The fact that Jumpers is a contemporary play and Candide is not caused me both to go to one and to avoid the other. Writing the best essay explains why Kate rather than Frank won the prize, since that is a causal difference between the two of them. So it appears that the reason some causes are not explanatory is that so many of our why‐questions are contrastive, and for these only causes that mark a difference between fact and foil will provide good answers.

4. Why Do Causes Explain?

An account of contrastive explanation can itself be seen as an answer to a philosophical contrastive question: why do some causes explain rather than others? But a good answer to this question may not explain why any causes explain, since it may simply presuppose that some causes do. To explain why any causes explain, we need to address different questions, which may also be contrastive, such as: why do causes rather than effects explain? For while some causes explain their effects, effects do not explain their causes. The recession of the galaxy explains why its light is red shifted, but the red shift does not explain why the galaxy is receding, even though the red shift may provide essential evidence of the recession, and either can be deduced from the other with the help of the Doppler law.

Do effects really never explain? Some good explanations appear at least superficially to be ‘effectal’. Thus biologists appear to explain the presence of a trait in terms of its function, which is one of its effects. Thus we may explain the coloration of the wings of a moth in terms of its function of providing camouflage. Camouflage explains coloration, but camouflage is an effect of the coloration. It has, however, been argued that this appearance of effectal explanation is misleading, because functional explanations are actually causal. According to this ‘selected effects’ view of functional explanation, because of the natural selection mechanism, what explains current coloration is past camouflage. This caused the current coloration, because of the enhanced fitness that previous moths with such coloration enjoyed. So citing camouflage is to cite a cause after all (Wright 1976 ; Allen, Bekoff, and Lauder 1998 ). Perhaps there are other more plausible examples of legitimate explanation by effect, such as explanations by appeal to least‐action principles in physics, but the explanatory asymmetry between cause and effect is very pronounced even if not quite universal, and an account of why this is so may help to show what makes causes explanatory.

The question as to why causes rather than effects explain is difficult to answer. It is difficult to avoid circular explanations, along the lines of, ‘causes explain because they, unlike effects, have the power to confer understanding’. Moreover, there is a clear sense in which finding out about a thing's effects does increase our understanding of that thing. Indeed it may be that P 's effects typically tell one more about P than do its causes. For effects often give information about P 's properties in a way that causes do not. This is so because physical properties are at least often dispositional, and dispositions are characterized by their effects and not by their causes. Thus to say that arsenic is poisonous is to say roughly that if you eat it you will die. The effects not only lead us back to the properties, but they are constitutive of at least some of them. In the conditional ‘If you eat it, then you will die’ there is both a cause and an effect, but they bear an asymmetrical relation to the corresponding property of being poisonous. Causing death is constitutive of the property of being poisonous, but eating arsenic, though a cause of death, is not constitutive of being poisonous. Nor do the causes of the arsenic or of its presence in a particular place appear to be constitutive of arsenic's properties. Yet the explanatory asymmetry between cause and effect still appears genuine: causes explain effects; effects do not explain causes.

A natural thought is that what is special about the causes of P is that they, unlike P 's effects, create or bring about P . Can this be the key to the explanatory asymmetry between causes and effects? But this may be another circular explanation. Why do causes explain effects? Because causes bring about effects. The worry is that ‘bring about’ is just another expression for ‘cause’, so all that has really been said is that causes explain because they are causes. A response would be to insist on a strong reading of ‘bring about’, a reading that would rule out a Humean account of causation, which takes causation to be no more than a constant conjunction or pattern of events.

Humeans may not like this, but they have the option of an error theory of explanation, according to which we never really explain why things happen, though the source of the illusion can be given, much as Hume himself had an error theory of necessary connection, according to which objects in the world are only conjoined, never connected, but the source of our mistaken idea of connection can be given. For Hume held that even though we cannot properly conceive of any connection between cause and effect, we nevertheless do have an idea of necessary connection. Hume traces that idea to the expectation we form of a familiar effect upon seeing a familiar cause. We then proceed illegitimately to project that feeling onto the world, supposing that the external cause and effect are themselves connected, in spite of absurdity of supposing that what connects one billiard ball to another on impact is a feeling of expectation ( 1748 : sect. 7). Applied to the notion of explanation, such an approach would allow the reality of causation as pattern, but would treat understanding as a kind of pervasive illusion, since it depends on a notion of causation that is metaphysically untenable. This would still be to allow that our notion of explanation and understanding, however misguided, depends on the idea of things being created, generated, or brought about by their causes.

Many would find such eliminativism about understanding unpalatable. But an appeal to the thought that explanation depends on powerful metaphysical ‘glue’ linking E 's cause to E as a way of explaining why causes rather than effects explain might also be problematic for two other reasons. First, as an account of causation strengthens the link between an event and its causes, it will do likewise for the connection between an event and its effects, so it is not clear that an appeal to a strong connection between cause and effect actually helps to account for the explanatory asymmetry. Secondly, many good explanations appeal to causes that may not be strongly connected to what they cause. This is illustrated by explanatory causes that are omissions. A good answer to the question of why Jane is eating her campfire meal with a stick is that she has no spoon, yet there seems no especially strong metaphysical glue between the absence of the spoon and the use of the stick.

A somewhat more promising answer to the question of why causes rather than effects explain appeals to the idea that only causes can make the difference between the phenomenon occurring and not occurring. This is connected to the idea of control, since effects are controlled through causes that make a difference, causes without which the effect would not occur. The causes of a phenomenon may be handles that could in principle have been used to prevent the phenomenon occurring in a way that the phenomenon's effects could not. To be sure, control is not always a practical option. The galaxy's recession causes and explains its red shift even though we are in no position to change its motion; but the speed of recession is nevertheless a cause that made the difference between that amount of red shift and another. This may partially account for why causes rather than effects explain, since causes often make a difference in this sense while effects never do. Information about causes provides a special kind of intellectual handle on phenomena because the causes may provide a kind of physical handle on those phenomena (cf. Woodward 2003 ).

One attraction of this view is that it may account for our ambivalence about the explanatory use of certain causes. For not all causes do make a difference. The obvious situation where they do not is one of overdetermination. An ecological example is an environment with foxes and rabbits (Garfinkel 1981 : 53–6). To the question as to why a rabbit was killed we may answer by giving the location of the guilty fox shortly before the deed, or we may cite the high fox population in the region. Both are causes, but the details of the guilty fox's behaviour do not explain well because, given the high fox population, had that fox not killed the rabbit, another fox probably would have. Had the fox population been substantially lower, by contrast, the rabbit probably would have survived. The cause that made the difference is the cause that explains. The idea that causes explain because they provide a kind of handle is thus closely related to the difference condition on contrastive explanation discussed above. So it may be that one reason that some causes explain while others do not is in the end the same as the reason those causes explain while effects do not. Neither effects nor undiscriminating causes make the sort of difference between the phenomenon occurring and not occurring that provides understanding.

5. Explanation and Causal Inference

As we have seen, the metaphysics of causation may illuminate explanation. In turn, explanation may illuminate the epistemology of causation. This is the idea behind Inference to the Best Explanation: explanatory considerations are a guide to causal inference (Lipton 2004 ). Causal inferences are non‐demonstrative, which means that there will always be competing causal hypotheses compatible with the same data. The suggestion is that we decide which of the competing hypotheses the evidence best supports by determining how well the competitors would explain that evidence. Many inferences are naturally described in this way. Seeing the ball next to the broken vase, the parent infers that the children have been playing catch in the house, because this is the best explanation of what the parent observes. Darwin inferred the hypothesis of natural selection because, although it was not entailed by his diverse biological evidence, the causal hypothesis of natural selection would provide the best explanation of that evidence. Astronomers infer that a galaxy is receding from the earth with a specified velocity, because the recession would be the best explanation of the observed red shift of the galaxy's characteristic spectrum. Detectives infer that it was Moriarty who committed the crime, because this hypothesis would best explain the fingerprints, blood stains, and other forensic evidence. Sherlock Holmes to the contrary, this is not a matter of deduction. The evidence will not entail that Moriarty is to blame, since it always remains possible that someone else was the perpetrator. Nevertheless, Holmes is right to make his inference, since Moriarty's guilt would provide a better explanation of the evidence than would anyone else's.

Inference to the Best Explanation can be seen as an extension of the idea of self‐evidencing explanations where the phenomenon that is explained in turn provides an essential part of the reason for believing the explanation is correct. For example, the speed of recession would cause and explain the red shift, but the observed red shift may at the same time be an essential part of the reason astronomers have for believing that the galaxy is receding at that speed. As we have seen, self‐evidencing explanations exhibit a curious circularity, but this circularity is benign. The recession is used to explain the red shift and the red shift is used to determine the recession, yet the recession hypothesis may be both explanatory and well supported. According to Inference to the Best Explanation, this is a common situation: hypotheses are supported by the very observations they are supposed to explain. Moreover, on this model, the observations support the hypothesis precisely because it would explain them.

Inference to the Best Explanation thus partially inverts an otherwise natural view of the relationship between causal inference and explanation. According to that natural view, the inference is prior to the explanation. First we must decide which hypotheses to accept; then, when called upon to explain some observation, we will draw from our pool of accepted hypotheses. According to Inference to the Best Explanation, by contrast, it is only by asking how well various hypotheses would explain the available evidence that we determine which hypotheses merit acceptance. In this sense, Inference to the Best Explanation has it that explanation is prior to inference.

Although it gives a natural account of many inferences in both science and ordinary life, the model needs further development. What, for example, should be meant by ‘best’? This is sometimes taken to mean likeliest or most plausible, but Inference to the Likeliest Explanation would be a disappointingly uninformative model, since the main point of an account of inference is to say what leads one hypothesis to be judged likelier than another, to give the symptoms of likeliness. A more promising approach construes ‘best’ as ‘loveliest’. On this view, we infer the hypothesis that would, if correct, provide the greatest causal understanding.

The model should thus be construed as ‘Inference to the Loveliest Explanation’. Its central claim is that loveliness is a guide to likeliness, that the explanation that would, if correct, provide the most understanding, is the explanation that is judged likeliest to be correct. This at least is not a trivial claim, but it faces at least three challenges. The first is to identify the explanatory virtues, the features of explanations that contribute to the degree of understanding they provide. There are a number of plausible candidates for the these virtues, including scope, precision, mechanism, unification, and simplicity. Better explanations explain more types of phenomena, explain them with greater precision, provide more information about underlying causal mechanisms, unify apparently disparate phenomena, or simplify our overall picture of the world. But analysing these and other explanatory virtues is not easy, and it also leaves the other two challenges. One of these is to show that these aspects of loveliness match judgements of likeliness, that the loveliest explanations tend also to be those that are judged likeliest to be correct. The remaining challenge is to show that, granting the match between loveliness and judgements of likeliness, the former is in fact our guide to the latter.

In addition to offering a description of an important aspect of causal inferences, Inference to the Best Explanation has been used to justify them, to show that those causal hypotheses judged likely to be correct really are so. For example, it has been argued that there is good reason to believe that the best scientific theories are true, since the truth of those theories is the best explanation of their wide‐ranging predictive success. Indeed it has been claimed that the successes of our best scientific theories would be inexplicable unless they was at least approximately true (Putnam 1978 : 18–22).

This argument has considerable plausibility; nevertheless, it faces serious objections. If scientific theories are themselves accepted on the basis of inferences to the best explanation, then to use an argument of the same form to show that those inferences lead to the truth may beg the question. Moreover, it is not clear that the truth of a theory really is the best explanation of its predictive success. For one thing, it seems no better an explanation than would be the truth of a competing theory that happens to share those particular predictions. For another, to explain why our current theories have so far been successful may not require an appeal to truth, if scientists have a policy of weeding out unsuccessful theories.

The explanation that the truth of a theory would provide for the truth of the predictions that the theory entails appears to be logical rather than causal. This may provide some answer to the circularity objection, since the first‐order scientific inferences that this overarching logical inference is supposed to warrant are at least predominantly causal. But it may also raise the suspicion that the real source of the plausibility of the argument is the plausibility of inferring from the premiss that most false causal hypotheses would have yielded false predictions to the conclusion that most causal hypotheses that yield true predictions are themselves true. Perhaps the premiss of this argument is correct, but the argument is fallacious. Most losing lottery tickets get the first three digits of the winning number wrong, but most tickets that get the first three digits right are losers too. It remains to be shown why the predictive successes of a general causal hypothesis is any better reason to believe that hypothesis is true than getting the first few digits of a lottery ticket right is a reason to think that ticket is a winner.

Further Reading

Lewis ( 1986 ) is an influential presentation of the view that to explain a phenomenon is to give information about its causal history. Lipton ( 2004 ) provides an accessible discussion of a causal model of explanation and of the idea that explanatory considerations are a guide to causal inference. Psillos ( 2002 ) is a clear introduction to causation, explanation, and the relations between the two. Salmon ( 1998 ) is a collection of essays on the relationship between causation and explanation by one of the most influential twentieth‐century figures in this field. Woodward ( 2003 ) is a recent and detailed account of the relationship between causation and explanation, emphasizing the importance of manipulation and control.

Allen, C. , Bekoff, M. , and Lauder, G. (eds.) ( 1998 ). Nature's Purposes . Cambridge, Mass.: MIT.

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Causal Hypothesis

In scientific research, understanding causality is key to unraveling the intricacies of various phenomena. A causal hypothesis is a statement that predicts a cause-and-effect relationship between variables in a study. It serves as a guide to study design, data collection, and interpretation of results. This thesis statement segment aims to provide you with clear examples of causal hypotheses across diverse fields, along with a step-by-step guide and useful tips for formulating your own. Let’s delve into the essential components of constructing a compelling causal hypothesis.

What is Causal Hypothesis?

A causal hypothesis is a predictive statement that suggests a potential cause-and-effect relationship between two or more variables. It posits that a change in one variable (the independent or cause variable) will result in a change in another variable (the dependent or effect variable). The primary goal of a causal hypothesis is to determine whether one event or factor directly influences another. This type of Simple hypothesis is commonly tested through experiments where one variable can be manipulated to observe the effect on another variable.

What is an example of a Causal Hypothesis Statement?

Example 1: If a person increases their physical activity (cause), then their overall health will improve (effect).

Explanation: Here, the independent variable is the “increase in physical activity,” while the dependent variable is the “improvement in overall health.” The hypothesis suggests that by manipulating the level of physical activity (e.g., by exercising more), there will be a direct effect on the individual’s health.

Other examples can range from the impact of a change in diet on weight loss, the influence of class size on student performance, or the effect of a new training method on employee productivity. The key element in all causal hypotheses is the proposed direct relationship between cause and effect.

100 Causal Hypothesis Statement Examples

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Causal hypotheses predict cause-and-effect relationships, aiming to understand the influence one variable has on another. Rooted in experimental setups, they’re essential for deriving actionable insights in many fields. Delve into these 100 illustrative examples to understand the essence of causal relationships.

• Dietary Sugar & Weight Gain: Increased sugar intake leads to weight gain.
• Exercise & Mental Health: Regular exercise improves mental well-being.
• Sleep & Productivity: Lack of adequate sleep reduces work productivity.
• Class Size & Learning: Smaller class sizes enhance student understanding.
• Smoking & Lung Disease: Regular smoking causes lung diseases.
• Pesticides & Bee Decline: Use of certain pesticides leads to bee population decline.
• Stress & Hair Loss: Chronic stress accelerates hair loss.
• Music & Plant Growth: Plants grow better when exposed to classical music.
• UV Rays & Skin Aging: Excessive exposure to UV rays speeds up skin aging.
• Reading & Vocabulary: Regular reading improves vocabulary breadth.
• Video Games & Reflexes: Playing video games frequently enhances reflex actions.
• Air Pollution & Respiratory Issues: High levels of air pollution increase respiratory diseases.
• Green Spaces & Happiness: Living near green spaces improves overall happiness.
• Yoga & Blood Pressure: Regular yoga practices lower blood pressure.
• Meditation & Stress Reduction: Daily meditation reduces stress levels.
• Social Media & Anxiety: Excessive social media use increases anxiety in teenagers.
• Alcohol & Liver Damage: Regular heavy drinking leads to liver damage.
• Training & Job Efficiency: Intensive training improves job performance.
• Seat Belts & Accident Survival: Using seat belts increases chances of surviving car accidents.
• Soft Drinks & Bone Density: High consumption of soft drinks decreases bone density.
• Homework & Academic Performance: Regular homework completion improves academic scores.
• Organic Food & Health Benefits: Consuming organic food improves overall health.
• Fiber Intake & Digestion: Increased dietary fiber enhances digestion.
• Therapy & Depression Recovery: Regular therapy sessions improve depression recovery rates.
• Financial Education & Savings: Financial literacy education increases personal saving rates.
• Brushing & Dental Health: Brushing teeth twice a day reduces dental issues.
• Carbon Emission & Global Warming: Higher carbon emissions accelerate global warming.
• Afforestation & Climate Stability: Planting trees stabilizes local climates.
• Ad Exposure & Sales: Increased product advertisement boosts sales.
• Parental Involvement & Academic Success: Higher parental involvement enhances student academic performance.
• Hydration & Skin Health: Regular water intake improves skin elasticity and health.
• Caffeine & Alertness: Consuming caffeine increases alertness levels.
• Antibiotics & Bacterial Resistance: Overuse of antibiotics leads to increased antibiotic-resistant bacteria.
• Pet Ownership & Loneliness: Having pets reduces feelings of loneliness.
• Fish Oil & Cognitive Function: Regular consumption of fish oil improves cognitive functions.
• Noise Pollution & Sleep Quality: High levels of noise pollution degrade sleep quality.
• Exercise & Bone Density: Weight-bearing exercises increase bone density.
• Vaccination & Disease Prevention: Proper vaccination reduces the incidence of related diseases.
• Laughter & Immune System: Regular laughter boosts the immune system.
• Gardening & Stress Reduction: Engaging in gardening activities reduces stress levels.
• Travel & Cultural Awareness: Frequent travel increases cultural awareness and tolerance.
• High Heels & Back Pain: Prolonged wearing of high heels leads to increased back pain.
• Junk Food & Heart Disease: Excessive junk food consumption increases the risk of heart diseases.
• Mindfulness & Anxiety Reduction: Practicing mindfulness lowers anxiety levels.
• Online Learning & Flexibility: Online education offers greater flexibility to learners.
• Urbanization & Wildlife Displacement: Rapid urbanization leads to displacement of local wildlife.
• Vitamin C & Cold Recovery: High doses of vitamin C speed up cold recovery.
• Team Building Activities & Work Cohesion: Regular team-building activities improve workplace cohesion.
• Multitasking & Productivity: Multitasking reduces individual task efficiency.
• Protein Intake & Muscle Growth: Increased protein consumption boosts muscle growth in individuals engaged in strength training.
• Mentoring & Career Progression: Having a mentor accelerates career progression.
• Fast Food & Obesity Rates: High consumption of fast food leads to increased obesity rates.
• Deforestation & Biodiversity Loss: Accelerated deforestation results in significant biodiversity loss.
• Language Learning & Cognitive Flexibility: Learning a second language enhances cognitive flexibility.
• Red Wine & Heart Health: Moderate red wine consumption may benefit heart health.
• Public Speaking Practice & Confidence: Regular public speaking practice boosts confidence.
• Fasting & Metabolism: Intermittent fasting can rev up metabolism.
• Plastic Usage & Ocean Pollution: Excessive use of plastics leads to increased ocean pollution.
• Peer Tutoring & Academic Retention: Peer tutoring improves academic retention rates.
• Mobile Usage & Sleep Patterns: Excessive mobile phone use before bed disrupts sleep patterns.
• Green Spaces & Mental Well-being: Living near green spaces enhances mental well-being.
• Organic Foods & Health Outcomes: Consuming organic foods leads to better health outcomes.
• Art Exposure & Creativity: Regular exposure to art boosts creativity.
• Gaming & Hand-Eye Coordination: Engaging in video games improves hand-eye coordination.
• Prenatal Music & Baby’s Development: Exposing babies to music in the womb enhances their auditory development.
• Dark Chocolate & Mood Enhancement: Consuming dark chocolate can elevate mood.
• Urban Farms & Community Engagement: Establishing urban farms promotes community engagement.
• Reading Fiction & Empathy Levels: Reading fiction regularly increases empathy.
• Aerobic Exercise & Memory: Engaging in aerobic exercises sharpens memory.
• Meditation & Blood Pressure: Regular meditation can reduce blood pressure.
• Classical Music & Plant Growth: Plants exposed to classical music show improved growth.
• Pollution & Respiratory Diseases: Higher pollution levels increase respiratory diseases’ incidence.
• Parental Involvement & Child’s Academic Success: Direct parental involvement in schooling enhances children’s academic success.
• Sugar Intake & Tooth Decay: High sugar intake is directly proportional to tooth decay.
• Physical Books & Reading Comprehension: Reading physical books improves comprehension better than digital mediums.
• Daily Journaling & Self-awareness: Maintaining a daily journal enhances self-awareness.
• Robotics Learning & Problem-solving Skills: Engaging in robotics learning fosters problem-solving skills in students.
• Forest Bathing & Stress Relief: Immersion in forest environments (forest bathing) reduces stress levels.
• Reusable Bags & Environmental Impact: Using reusable bags reduces environmental pollution.
• Affirmations & Self-esteem: Regularly reciting positive affirmations enhances self-esteem.
• Local Produce Consumption & Community Economy: Buying and consuming local produce boosts the local economy.
• Sunlight Exposure & Vitamin D Levels: Regular sunlight exposure enhances Vitamin D levels in the body.
• Group Study & Learning Enhancement: Group studies can enhance learning compared to individual studies.
• Active Commuting & Fitness Levels: Commuting by walking or cycling improves overall fitness.
• Foreign Film Watching & Cultural Understanding: Watching foreign films increases understanding and appreciation of different cultures.
• Craft Activities & Fine Motor Skills: Engaging in craft activities enhances fine motor skills.
• Listening to Podcasts & Knowledge Expansion: Regularly listening to educational podcasts broadens one’s knowledge base.
• Outdoor Play & Child’s Physical Development: Encouraging outdoor play accelerates physical development in children.
• Thrift Shopping & Sustainable Living: Choosing thrift shopping promotes sustainable consumption habits.
• Nature Retreats & Burnout Recovery: Taking nature retreats aids in burnout recovery.
• Virtual Reality Training & Skill Acquisition: Using virtual reality for training accelerates skill acquisition in medical students.
• Pet Ownership & Loneliness Reduction: Owning a pet significantly reduces feelings of loneliness among elderly individuals.
• Intermittent Fasting & Metabolism Boost: Practicing intermittent fasting can lead to an increase in metabolic rate.
• Bilingual Education & Cognitive Flexibility: Being educated in a bilingual environment improves cognitive flexibility in children.
• Urbanization & Loss of Biodiversity: Rapid urbanization contributes to a loss of biodiversity in the surrounding environment.
• Recycled Materials & Carbon Footprint Reduction: Utilizing recycled materials in production processes reduces a company’s overall carbon footprint.
• Artificial Sweeteners & Appetite Increase: Consuming artificial sweeteners might lead to an increase in appetite.
• Green Roofs & Urban Temperature Regulation: Implementing green roofs in urban buildings contributes to moderating city temperatures.
• Remote Work & Employee Productivity: Adopting a remote work model can boost employee productivity and job satisfaction.
• Sensory Play & Child Development: Incorporating sensory play in early childhood education supports holistic child development.

Causal Hypothesis Statement Examples in Research

Research hypothesis often delves into understanding the cause-and-effect relationships between different variables. These causal hypotheses attempt to predict a specific effect if a particular cause is present, making them vital for experimental designs.

• Artificial Intelligence & Job Market: Implementation of artificial intelligence in industries causes a decline in manual jobs.
• Online Learning Platforms & Traditional Classroom Efficiency: The introduction of online learning platforms reduces the efficacy of traditional classroom teaching methods.
• Nano-technology & Medical Treatment Efficacy: Using nano-technology in drug delivery enhances the effectiveness of medical treatments.
• Genetic Editing & Lifespan: Advancements in genetic editing techniques directly influence the lifespan of organisms.
• Quantum Computing & Data Security: The rise of quantum computing threatens the security of traditional encryption methods.
• Space Tourism & Aerospace Advancements: The demand for space tourism propels advancements in aerospace engineering.
• E-commerce & Retail Business Model: The surge in e-commerce platforms leads to a decline in the traditional retail business model.
• VR in Real Estate & Buyer Decisions: Using virtual reality in real estate presentations influences buyer decisions more than traditional methods.
• Biofuels & Greenhouse Gas Emissions: Increasing biofuel production directly reduces greenhouse gas emissions.
• Crowdfunding & Entrepreneurial Success: The availability of crowdfunding platforms boosts the success rate of start-up enterprises.

Causal Hypothesis Statement Examples in Epidemiology

Epidemiology is a study of how and why certain diseases occur in particular populations. Causal hypotheses in this field aim to uncover relationships between health interventions, behaviors, and health outcomes.

• Vaccine Introduction & Disease Eradication: The introduction of new vaccines directly leads to the reduction or eradication of specific diseases.
• Urbanization & Rise in Respiratory Diseases: Increased urbanization causes a surge in respiratory diseases due to pollution.
• Processed Foods & Obesity Epidemic: The consumption of processed foods is directly linked to the rising obesity epidemic.
• Sanitation Measures & Cholera Outbreaks: Implementing proper sanitation measures reduces the incidence of cholera outbreaks.
• Tobacco Consumption & Lung Cancer: Prolonged tobacco consumption is the primary cause of lung cancer among adults.
• Antibiotic Misuse & Antibiotic-Resistant Strains: Misuse of antibiotics leads to the evolution of antibiotic-resistant bacterial strains.
• Alcohol Consumption & Liver Diseases: Excessive and regular alcohol consumption is a leading cause of liver diseases.
• Vitamin D & Rickets in Children: A deficiency in vitamin D is the primary cause of rickets in children.
• Airborne Pollutants & Asthma Attacks: Exposure to airborne pollutants directly triggers asthma attacks in susceptible individuals.
• Sedentary Lifestyle & Cardiovascular Diseases: Leading a sedentary lifestyle is a significant risk factor for cardiovascular diseases.

Causal Hypothesis Statement Examples in Psychology

In psychology, causal hypotheses explore how certain behaviors, conditions, or interventions might influence mental and emotional outcomes. These hypotheses help in deciphering the intricate web of human behavior and cognition.

• Childhood Trauma & Personality Disorders: Experiencing trauma during childhood increases the risk of developing personality disorders in adulthood.
• Positive Reinforcement & Skill Acquisition: The use of positive reinforcement accelerates skill acquisition in children.
• Sleep Deprivation & Cognitive Performance: Lack of adequate sleep impairs cognitive performance in adults.
• Social Isolation & Depression: Prolonged social isolation is a significant cause of depression among teenagers.
• Mindfulness Meditation & Stress Reduction: Regular practice of mindfulness meditation reduces symptoms of stress and anxiety.
• Peer Pressure & Adolescent Risk Taking: Peer pressure significantly increases risk-taking behaviors among adolescents.
• Parenting Styles & Child’s Self-esteem: Authoritarian parenting styles negatively impact a child’s self-esteem.
• Multitasking & Attention Span: Engaging in multitasking frequently leads to a reduced attention span.
• Childhood Bullying & Adult PTSD: Individuals bullied during childhood have a higher likelihood of developing PTSD as adults.
• Digital Screen Time & Child Development: Excessive digital screen time impairs cognitive and social development in children.

Causal Inference Hypothesis Statement Examples

Causal inference is about deducing the cause-effect relationship between two variables after considering potential confounders. These hypotheses aim to find direct relationships even when other influencing factors are present.

• Dietary Habits & Chronic Illnesses: Even when considering genetic factors, unhealthy dietary habits increase the chances of chronic illnesses.
• Exercise & Mental Well-being: When accounting for daily stressors, regular exercise improves mental well-being.
• Job Satisfaction & Employee Turnover: Even when considering market conditions, job satisfaction inversely relates to employee turnover.
• Financial Literacy & Savings Behavior: When considering income levels, financial literacy is directly linked to better savings behavior.
• Online Reviews & Product Sales: Even accounting for advertising spends, positive online reviews boost product sales.
• Prenatal Care & Child Health Outcomes: When considering genetic factors, adequate prenatal care ensures better health outcomes for children.
• Teacher Qualifications & Student Performance: Accounting for socio-economic factors, teacher qualifications directly influence student performance.
• Community Engagement & Crime Rates: When considering economic conditions, higher community engagement leads to lower crime rates.
• Eco-friendly Practices & Brand Loyalty: Accounting for product quality, eco-friendly business practices boost brand loyalty.
• Mental Health Support & Workplace Productivity: Even when considering workload, providing mental health support enhances workplace productivity.

What are the Characteristics of Causal Hypothesis

Causal hypotheses are foundational in many research disciplines, as they predict a cause-and-effect relationship between variables. Their unique characteristics include:

• Cause-and-Effect Relationship: The core of a causal hypothesis is to establish a direct relationship, indicating that one variable (the cause) will bring about a change in another variable (the effect).
• Testability: They are formulated in a manner that allows them to be empirically tested using appropriate experimental or observational methods.
• Specificity: Causal hypotheses should be specific, delineating clear cause and effect variables.
• Directionality: They typically demonstrate a clear direction in which the cause leads to the effect.
• Operational Definitions: They often use operational definitions, which specify the procedures used to measure or manipulate variables.
• Temporal Precedence: The cause (independent variable) always precedes the effect (dependent variable) in time.

What is a causal hypothesis in research?

In research, a causal hypothesis is a statement about the expected relationship between variables, or explanation of an occurrence, that is clear, specific, testable, and falsifiable. It suggests a relationship in which a change in one variable is the direct cause of a change in another variable. For instance, “A higher intake of Vitamin C reduces the risk of common cold.” Here, Vitamin C intake is the independent variable, and the risk of common cold is the dependent variable.

What is the difference between causal and descriptive hypothesis?

• Causal Hypothesis: Predicts a cause-and-effect relationship between two or more variables.
• Descriptive Hypothesis: Describes an occurrence, detailing the characteristics or form of a particular phenomenon.
• Causal: Consuming too much sugar can lead to diabetes.
• Descriptive: 60% of adults in the city exercise at least thrice a week.
• Causal: To establish a causal connection between variables.
• Descriptive: To give an accurate portrayal of the situation or fact.
• Causal: Often involves experiments.
• Descriptive: Often involves surveys or observational studies.

How do you write a Causal Hypothesis? – A Step by Step Guide

• Identify Your Variables: Pinpoint the cause (independent variable) and the effect (dependent variable). For instance, in studying the relationship between smoking and lung health, smoking is the independent variable while lung health is the dependent variable.
• State the Relationship: Clearly define how one variable affects another. Does an increase in the independent variable lead to an increase or decrease in the dependent variable?
• Be Specific: Avoid vague terms. Instead of saying “improved health,” specify the type of improvement like “reduced risk of cardiovascular diseases.”
• Use Operational Definitions: Clearly define any terms or variables in your hypothesis. For instance, define what you mean by “regular exercise” or “high sugar intake.”
• Ensure It’s Testable: Your hypothesis should be structured so that it can be disproven or supported by data.
• Review Existing Literature: Check previous research to ensure that your hypothesis hasn’t already been tested, and to ensure it’s plausible based on existing knowledge.
• Draft Your Hypothesis: Combine all the above steps to write a clear, concise hypothesis. For instance: “Regular exercise (defined as 150 minutes of moderate exercise per week) decreases the risk of cardiovascular diseases.”

Tips for Writing Causal Hypothesis

• Simplicity is Key: The clearer and more concise your hypothesis, the easier it will be to test.
• Avoid Absolutes: Using words like “all” or “always” can be problematic. Few things are universally true.
• Seek Feedback: Before finalizing your hypothesis, get feedback from peers or mentors.
• Stay Objective: Base your hypothesis on existing literature and knowledge, not on personal beliefs or biases.
• Revise as Needed: As you delve deeper into your research, you may find the need to refine your hypothesis for clarity or specificity.
• Falsifiability: Always ensure your hypothesis can be proven wrong. If it can’t be disproven, it can’t be validated either.
• Avoid Circular Reasoning: Ensure that your hypothesis doesn’t assume what it’s trying to prove. For example, “People who are happy have a positive outlook on life” is a circular statement.
• Specify Direction: In causal hypotheses, indicating the direction of the relationship can be beneficial, such as “increases,” “decreases,” or “leads to.”

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• Volume 58, Issue 4
• A definition of causal effect for epidemiological research
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• Correspondence to:
 Dr M Hernán
 Department of Epidemiology, Harvard School of Public Health, 677 Huntington Avenue, Boston, MA 02115, USA; miguel_hernanpost.harvard.edu

Estimating the causal effect of some exposure on some outcome is the goal of many epidemiological studies. This article reviews a formal definition of causal effect for such studies. For simplicity, the main description is restricted to dichotomous variables and assumes that no random error attributable to sampling variability exists. The appendix provides a discussion of sampling variability and a generalisation of this causal theory. The difference between association and causation is described—the redundant expression “causal effect” is used throughout the article to avoid confusion with a common use of “effect” meaning simply statistical association—and shows why, in theory, randomisation allows the estimation of causal effects without further assumptions. The article concludes with a discussion on the limitations of randomised studies. These limitations are the reason why methods for causal inference from observational data are needed.

https://doi.org/10.1136/jech.2002.006361

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INDIVIDUAL CAUSAL EFFECTS

Zeus is a patient waiting for a heart transplant. On 1 January, he received a new heart. Five days later, he died. Imagine that we can somehow know, perhaps by divine revelation, that had Zeus not received a heart transplant on 1 January (all others things in his life being unchanged) then he would have been alive five days later. Most people equipped with this information would agree that the transplant caused Zeus’ death. The intervention had a causal effect on Zeus’ five day survival.

Another patient, Hera, received a heart transplant on 1 January. Five days later she was alive. Again, imagine we can somehow know that had Hera not received the heart on 1 January (all other things being equal) then she would still have been alive five days later. The transplant did not have a causal effect on Hera’s five day survival.

These two vignettes illustrate how human reasoning for causal inference works: we compare (often only mentally) the outcome when action A is present with the outcome when action A is absent, all other things being equal. If the two outcomes differ, we say that the action A has a causal effect, causative or preventive, on the outcome. Otherwise, we say that the action A has no causal effect on the outcome. In epidemiology, A is commonly referred to as exposure or treatment.

The next step is to make this causal intuition of ours amenable to mathematical and statistical analysis by introducing some notation. Consider a dichotomous exposure variable A (1: exposed, 0: unexposed) and a dichotomous outcome variable Y (1: death, 0: survival). Table 1 shows the data from a heart transplant observational study with 20 participants. Let Y a  = 1 be the outcome variable that would have been observed under the exposure value a  = 1, and Y a  = 0 the outcome variable that would have been observed under the exposure value a  = 0. (Lowercase a represents a particular value of the variable A .) As shown in table 2, Zeus has Y a  = 1  = 1 and Y a  = 0  = 0 because he died when exposed but would have survived if unexposed.

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Data from a study with dichotomous exposure A and outcome Y

Counterfactual outcomes of subjects in a study with dichotomous exposure A and outcome Y

We are now ready to provide a formal definition of causal effect for each person: exposure has a causal effect if Y a  = 0 ≠ Y a  = 1 . Table 2 is all we need to decide that the exposure has an effect on Zeus’ outcome because Y a  = 0 ≠ Y a  = 1 , but not on Hera’s outcome because Y a  = 0  =  Y a  = 1 . When the exposure has no causal effect for any subject—that is, Y a  = 0  =  Y a  = 1 for all subjects—we say that the sharp causal null hypothesis is true.

The variables Y a  = 1 and Y a  = 0 are known as potential outcomes because one of them describes the subject’s outcome value that would have been observed under a potential exposure value that the subject did not actually experience. For example, Y a  = 0 is a potential outcome for exposed Zeus, and Y a  = 1 is a potential outcome for unexposed Hera. Because these outcomes would have been observed in situations that did not actually happen (that is, in counter to the fact situations), they are also known as counterfactual outcomes . For each subject, one of the counterfactual outcomes is actually factual—the one that corresponds to the exposure level or treatment regimen that the subject actually received. For example, if A  = 1 for Zeus, then Y a  = 1  =  Y a  =  A  =  Y for him.

The fundamental problem of causal inference should now be clear. Individual causal effects are defined as a contrast of the values of counterfactual outcomes, but only one of those values is observed. Table 3 shows the observed data and each subject’s observed counterfactual outcome: the one corresponding to the exposure value actually experienced by the subject. All other counterfactual outcomes are missing. The unhappy conclusion is that, in general, individual causal effects cannot be identified because of missing data.

Data and observed counterfactual outcomes from a study with dichotomous exposure A and outcome Y

POPULATION CAUSAL EFFECT

We define the probability Pr[ Y a  = 1] as the proportion of subjects that would have developed the outcome Y had all subjects in the population of interest received exposure value a . We also refer to Pr[ Y a  = 1] as the risk of Y a . The exposure has a causal effect in the population if Pr[ Y a  = 1  = 1]≠Pr[ Y a  = 0  = 1].

Suppose that our population is comprised by the subjects in table 2. Then Pr[ Y a  = 1  = 1] = 10/20 = 0.5, and Pr[ Y a  = 0  = 1] = 10/20 = 0.5. That is, 50% of the patients would have died had everybody received a heart transplant, and 50% would have died had nobody received a heart transplant. The exposure has no effect on the outcome at the population level. When the exposure has no causal effect in the population, we say that the causal null hypothesis is true.

Unlike individual causal effects, population causal effects can sometimes be computed—or, more rigorously, consistently estimated (see appendix)—as discussed below. Hereafter we refer to the “population causal effect” simply as “causal effect”. Some equivalent definitions of causal effect are

Pr[ Y a  = 1  = 1]−Pr[ Y a  = 0  = 1]≠0

Pr[ Y a  = 1  = 1]/Pr[ Y a  = 0  = 1]≠1

(Pr[ Y a  = 1  = 1]/Pr[ Y a  = 1  = 0])/(Pr[ Y a  = 0  = 1]/Pr[ Y a  = 0  = 0])≠1

where the left hand side of inequalities (a), (b), and (c) is the causal risk difference, risk ratio, and odds ratio, respectively. The causal risk difference, risk ratio, and odds ratio (and other causal parameters) can also be used to quantify the strength of the causal effect when it exists. They measure the same causal effect in different scales, and we refer to them as effect measures .

ASSOCIATION AND CAUSATION

To characterise association, we first define the probability Pr[ Y  = 1| A  =  a ] as the proportion of subjects that developed the outcome Y among those subjects in the population of interest that happened to receive exposure value a . We also refer to Pr[ Y  = 1| A  =  a ] as the risk of Y given A  =  a . Exposure and outcome are associated if Pr[ Y  = 1| A  = 1]≠Pr[ Y  = 1| A  = 0]. In our population of table 1, exposure and outcome are associated because Pr[ Y  = 1| A  = 1] = 7/13, and Pr[ Y  = 1| A  = 0] = 3/7. Some equivalent definitions of association are

Pr[ Y  = 1| A  = 1]−Pr[ Y  = 1| A  = 0]≠0

Pr[ Y  = 1| A  = 1]/Pr[ Y  = 1| A  = 0]≠1

(Pr[ Y  = 1| A  = 1]/Pr[ Y  = 0| A  = 1])/(Pr[ Y  = 1| A  = 0]/Pr[ Y  = 0| A  = 0])≠1

where the left hand side of the inequalities (a), (b), and (c) is the associational risk difference, risk ratio, and odds ratio, respectively. The associational risk difference, risk ratio, and odds ratio (and other association parameters) can also be used to quantify the strength of the association when it exists. They measure the same association in different scales, and we refer to them as association measures .

When A and Y are not associated, we say that A does not predict Y , or vice versa. Lack of association is represented by Y ⨿ A (or, equivalently, A ⨿ Y ), which is read as Y and A are independent.

Note that the risk Pr[ Y  = 1| A  =  a ] is computed using the subset of subjects of the population that meet the condition “having actually received exposure a ” (that is, it is a conditional probability), whereas the risk Pr[ Y a  = 1] is computed using all subjects of the population had they received the counterfactual exposure a (that is, it is an unconditional or marginal probability). Therefore, association is defined by a different risk in two disjoint subsets of the population determined by the subjects’ actual exposure value, whereas causation is defined by a different risk in the same subset (for example, the entire population) under two potential exposure values (fig 1). This radically different definition accounts for the well known adage “association is not causation.” When an association measure differs from the corresponding effect measure, we say that there is bias or confounding .

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Causation is defined by a different risk in the entire population under two potential exposure values; association is defined by a different risk in the subsets of the population determined by the subjects’ actual exposure value.

COMPUTATION OF CAUSAL EFFECTS VIA RANDOMISATION

Unlike association measures, effect measures cannot be directly computed because of missing data (see table 3). However, effect measures can be computed—or, more rigorously, consistently estimated (see appendix)—in randomised experiments.

Suppose we have a (near-infinite) population and that we flip a coin for each subject in such population. We assign the subject to group 1 if the coin turns tails, and to group 2 if it turns heads. Next we administer the treatment or exposure of interest ( A  = 1) to subjects in group 1 and placebo ( A  = 0) to those in group 2. Five days later, at the end of the study, we compute the mortality risks in each group, Pr[ Y  = 1| A  = 1] and Pr[ Y  = 1| A  = 0]. For now, let us assume that this randomised experiment is ideal in all other respects (no loss to follow up, full compliance with assigned treatment, blind assignment).

We will show that, in such a study, the observed risk Pr[ Y  = 1| A  =  a ] is equal to the counterfactual risk Pr[ Y a  = 1], and therefore the associational risk ratio equals the causal risk ratio.

First note that, when subjects are randomly assigned to groups 1 and 2, the proportion of deaths among the exposed, Pr[ Y  = 1| A  = 1], will be the same whether subjects in group 1 receive the exposure and subjects in group 2 receive placebo, or vice versa. Because group membership is randomised, both groups are “comparable”: which particular group got the exposure is irrelevant for the value of Pr[ Y  = 1| A  = 1]. (The same reasoning applies to Pr[ Y  = 1| A  = 0].) Formally, we say that both groups are exchangeable.

Exchangeability means that the risk of death in group 1 would have been the same as the risk of death in group 2 had subjects in group 1 received the exposure given to those in group 2. That is, the risk under the potential exposure value a among the exposed, Pr[ Y a  = 1| A  = 1], equals the risk under the potential exposure value a among the unexposed, Pr[ Y a  = 1| A  = 0], for a  = 0 and a  = 1. An obvious consequence of these (conditional) risks being equal in all subsets defined by exposure status in the population is that they must be equal to the (marginal) risk under exposure value a in the whole population: Pr[ Y a  = 1| A  = 1] = Pr[ Y a  = 1| A  = 0] = Pr[ Y a  = 1]. In other words, under exchangeability, the actual exposure does not predict the counterfactual outcome; they are independent, or Y a ⨿ A for all values a . Randomisation produces exchangeability.

We are only one step short of showing that the observed risk Pr[ Y  = 1| A  =  a ] equals the counterfactual risk Pr[ Y a  = 1] in ideal randomised experiments. By definition, the value of the counterfactual outcome Y a for subjects who actually received exposure value a is their observed outcome value Y . Then, among those who actually received exposure value a , the risk under the potential exposure value a is trivially equal to the observed risk. That is, Pr[ Y a  = 1| A  =  a ] = Pr[ Y  = 1| A  =  a ].

Let us now combine the results from the two previous paragraphs. Under exchangeability, Y a ⨿ A for all a , the conditional risk among those exposed to a is equal to the marginal risk had the whole population been exposed to a : Pr[ Y a  = 1| A  = 1] = Pr[ Y a  = 1| A  = 0] = Pr[ Y a  = 1]. And by definition of counterfactual outcome Pr[ Y a  = 1| A  =  a ] = Pr[ Y  = 1| A  =  a ]. Therefore, the observed risk Pr[ Y  = 1| A  =  a ] equals the counterfactual risk Pr[ Y a  = 1]. In ideal randomised experiments, association is causation. On the other hand, in non-randomised (for example, observational) studies association is not necessarily causation because of potential lack of exchangeability of exposed and unexposed subjects. For example, in our heart transplant study, the risk of death under no treatment is different for the exposed and the unexposed: Pr[ Y a  = 0  = 1| A  = 1] = 7/13≠Pr[ Y a  = 0  = 1| A  = 0] = 3/7. We say that the exposed had a worse prognosis, and therefore a greater risk of death, than the unexposed, or that Y a A does not hold for a  = 0.

INTERVENTIONS AND CAUSAL QUESTIONS

We have so far assumed that the counterfactual outcomes Y a exist and are well defined. However, that is not always the case.

Suppose women ( S  = 1) have a greater risk of certain disease Y than men ( S  = 0)—that is, Pr[ Y  = 1| S  = 1]>Pr[ Y  = 1| S  = 0]. Does sex S has a causal effect on the risk of Y— that is, Pr[ Y s  = 1  = 1]>Pr[ Y s  = 0  = 1]? This question is quite vague because it is unclear what we mean by the risk of Y had everybody been a woman (or a man). Do we mean the risk of Y had everybody “carried a pair of X chromosomes”, “been brought up as a woman”, “had female genitalia”, or “had high levels of oestrogens between adolescence and menopausal age”? Each of these definitions of the exposure “female sex” would lead to a different causal effect.

To give an unambiguous meaning to a causal question, we need to be able to describe the interventions that would allow us to compute the causal effect in an ideal randomised experiment. For example, “administer 30 μg/day of ethinyl estradiol from age 14 to age 45” compared with “administer placebo.” That some interventions sound technically unfeasible or plainly crazy simply indicates that the formulation of certain causal questions (for example, the effect of sex, high serum LDL-cholesterol, or high HIV viral load on the risk of certain disease) is not always straightforward. A counterfactual approach to causal inference highlights the imprecision of ambiguous causal questions, and the need for a common understanding of the interventions involved.

LIMITATIONS OF RANDOMISED EXPERIMENTS

We now review some common methodological problems that may lead to bias in randomised experiments. To fix ideas, suppose we are interested in the causal effect of a heart transplant on one year survival. We start with a (near-infinite) population of potential recipients of a transplant, randomly allocate each subject in the population to either transplant ( A  = 1) or medical treatment ( A  = 0), and ascertain how many subjects die within the next year ( Y  = 1) in each group. We then try to measure the effect of heart transplant on survival by computing the associational risk ratio Pr[ Y  = 1| A  = 1]/Pr[ Y  = 1| A  = 0], which is theoretically equal to the causal risk ratio Pr[ Y a  = 1  = 1]/Pr[ Y a  = 0  = 1]. Consider the following problems:

Loss to follow up . Subjects may be lost to follow up or drop out of the study before their outcome is ascertained. When this happens, the risk Pr[ Y  = 1| A  =  a ] cannot be computed because the value of Y is not available for some people. Instead we can compute Pr[ Y  = 1| A  =  a , C  = 0] where C indicates whether the subject was lost (1: yes, 0: no). This restriction to subjects with C  = 0 is problematic because subjects that were lost ( C  = 1) may not be exchangeable with subjects who remained through the end of the study ( C  = 0). For example, if subjects who did not receive a transplant ( A  = 0) and who had a more severe disease decide to leave the study, then the risk Pr[ Y  = 1| A  = 0, C  = 0] among those remaining in the study would be lower than the risk Pr[ Y  = 1| A  = 0] among those originally assigned to medical treatment. Our association measure Pr[ Y  = 1| A  = 1, C  = 0]/Pr[ Y  = 1| A  = 0, C  = 0] would not generally equal the effect measure Pr[ Y a  = 1  = 1]/Pr[ Y a  = 0  = 1].

Non-compliance . Subjects may not adhere to the assigned treatment. Let A be the exposure to which subjects were randomly assigned, and B the exposure they actually received. Suppose some subjects that had been assigned to medical treatment ( A  = 0) obtained a heart transplant outside of the study ( B  = 1). In an “intention to treat” analysis, we compute Pr[ Y  = 1| A  =  a ], which equals Pr[ Y a  = 1]. However, we are not interested in the causal effect of assignment A , a misclassified version of the true exposure B , but on the causal effect of B itself. The alternative “as treated” approach—using Pr[ Y  = 1| B  =  b ] for causal inference—is problematic. For example, if the most severely ill subjects in the A  = 0 group seek a heart transplant ( B  = 1) outside of the study, then the group B  = 1 would include a higher proportion of severely ill subjects than the group B  = 0. The groups B  = 1 and B  = 0 would not be exchangeable—that is, Pr[ Y  = 1| B  =  b ]≠Pr[ Y b  = 1]. In the presence of non-compliance, an intention to treat analysis guarantees exchangeability of the groups defined by a misclassified exposure (the original assignment), whereas an as treated analysis guarantees a correct classification of exposure but not exchangeability of the groups defined by this exposure. However, the intention to treat analysis is often preferred because, unlike the as treated analysis, it provides an unbiased association measure if the sharp causal null hypothesis holds for the exposure B .

Unblinding . When the study subjects are aware of the treatment they receive (as in our heart transplant study), they may change their behaviour accordingly. For example, those who received a transplant may change their diet to keep their new heart healthy. The equality Pr[ Y  = 1| A  =  a ] = Pr[ Y a  = 1] still holds, but now the causal effect of A combines the effects of the transplant and the dietary change. To avoid this problem, knowledge of the level of exposure assigned to each group is withheld from subjects and their doctors (they are “blinded”), when possible. The goal is to ensure that the whole effect, if any, of the exposure assignment A is solely attributable to the exposure received B (the heart transplant in our example). When this goal is achieved, we say that the exclusion restriction holds—that is, Y a  = 0, b  =  Y a  = 1, b for all subjects and all values b and, specifically, for the value B observed for each subject. In non-blinded studies, or when blinding does not work (for example, the well known side effects of a treatment make apparent who is taking it), the exclusion restriction cannot be guaranteed, and therefore the intention to treat analysis may not yield an unbiased association measure even under the sharp causal null hypothesis for exposure B .

In summary, the fact that exchangeability Y a ⨿ A holds in a well designed randomised experiment does not guarantee an unbiased estimate of the causal effect because: i ) Y may not be measured for all subjects (loss to follow up), ii ) A may be a misclassified version of the true exposure (non-compliance), and iii ) A may be a combination of the exposure of interest plus other actions (unblinding). Causal inference from randomised studies in the presence of these problems requires similar assumptions and analytical methods as causal inference from observational studies.

Leaving aside these methodological problems, randomised experiments may be unfeasible because of ethical, logistic, or financial reasons. For example, it is questionable that an ethical committee would have approved our heart transplant study. Hearts are in short supply and society favours assigning them to subjects who are more likely to benefit from the transplant, rather than assigning them randomly among potential recipients. Randomised experiments of harmful exposures (for example, cigarette smoking) are generally unacceptable too. Frequently, the only option is conducting observational studies in which exchangeability is not guaranteed.

BIBLIOGRAPHICAL NOTES

Hume 1 hinted a counterfactual theory of causation, but the application of counterfactual theory to the estimation of causal effects via randomised experiments was first formally proposed by Neyman. 2 Rubin 3, 4 extended Neyman’s theory to the estimation of the effects of fixed exposures in randomised and observational studies. Fixed exposures are exposures that either are applied at one point in time only or never change over time. Examples of fixed exposures in epidemiology are a surgical intervention, a traffic accident, a one dose immunisation, or a medical treatment that is continuously administered during a given period regardless of its efficacy or side effects. Rubin’s counterfactual model has been discussed by Holland and others. 5

Robins 6, 7 proposed a more general counterfactual model that permits the estimation of total and direct effects of fixed and time varying exposures in longitudinal studies, whether randomised or observational. Examples of time varying exposures in epidemiology are a medical treatment, diet, cigarette smoking, or an occupational exposure. For simplicity of presentation, our article was restricted to the effects of fixed exposures. The use of the symbol ⨿ to denote independence was introduced by Dawid. 8

A1 SAMPLING VARIABILITY

Our descriptions of causal effect and exchangeability have relied on the idea that we somehow collected information from all the subjects in the population of interest. This simplification has been useful to focus our attention on the conceptual aspects of causal inference, by keeping them separate from aspects related to random statistical variability. We now extend our definitions to more realistic settings in which random variability exists.

Many real world studies are based on samples of the population of interest. The first consequence of working with samples is that, even if the counterfactual outcomes of all subjects in the study were known, one cannot obtain the exact proportion of subjects in the population who had the outcome under exposure value a —that is, the probability Pr[ Y a  = 0  = 1] cannot be directly computed. One can only estimate this probability. Consider the subjects in table 2. We have previously viewed them as forming a 20 person population. Let us now view them as a random sample of a much larger population. In this sample, the proportion of subjects who would have died if unexposed is P̂r[ Y a −0  = 1]  = 10/20 = 0.5, which does not have to be exactly equal to the proportion of subjects who would have died if the entire population had been unexposed, Pr[ Y a  = 0  = 1]. We use the sample proportion P̂r[ Y a  = 1] to estimate the population probability Pr[ Y a  = 1]. (The “hat” over Pr indicates that P̂r[ Y a  = 1] is an estimator.) We say that P̂r[ Y a  = 1] is a consistent estimator of Pr[ Y a  = 1] because the larger the number of subjects in the sample, the smaller the difference between P̂r[ Y a  = 1] and Pr[ Y a  = 1] is expected to be. In the long run (that is, if the estimator is applied to infinite samples of the population), the mean difference is expected to become zero.

There is a causal effect of A on Y in such population if Pr[ Y a  = 1  = 1]≠Pr[ Y a  = 0  = 1]. This definition, however, cannot be directly applied because the population probabilities Pr[ Y a  = 1] cannot be computed, but only consistently estimated by the sample proportions P̂r[ Y a  = 1]. Therefore, one cannot conclude with certainty that there is (or there is not) a causal effect. Rather, standard statistical procedures are needed to test the causal null hypothesis Pr[ Y a  = 1  = 1] = Pr[ Y a  = 0  = 1] by comparing P̂r[ Y a −1  = 1] and P̂r[ Y a −1  = 1], and to compute confidence intervals for the effect measures. The availability of data from only a sample of subjects in the population, even if the values of all their counterfactual outcomes were known, is the first reason why statistics is necessary in causal inference.

The previous discussion assumes that one can have access to the values of both counterfactual outcomes for each subject in the sample (as in table 2), whereas in real world studies one can only access the value of one counterfactual outcome for each subject (as in table 3). Therefore, whether one is working with the whole population or with a sample, neither the probability Pr[ Y a  = 1] or its consistent estimator P̂r[ Y a  = 1] can be directly computed for any value a . Instead, one can compute the sample proportion of subjects that develop the outcome among the exposed, P̂r[ Y  = 1| A  = 1] = 7/13, and among the unexposed, P̂r[ Y  = 1| A  = 0] = 3/7. There are two major conceptualisations of this problem:

The population of interest is near infinite and we hypothesise that all subjects in the population are randomly assigned to either A  = 1 or A  = 0. Exchangeability of the exposed and unexposed would hold in the population—that is, Pr[ Y a  = 1] = Pr[ Y  = 1| A  =  a ]. Now we can see our sample as a random sample from this population where exposure is randomly assigned. The problem boils down to standard statistical inference with the sample proportion P̂r[ Y  = 1| A  =  a ] being a consistent estimator of the population probability Pr[ Y  = 1| A  =  a ]. This is the simplest conceptualisation.

Only the subjects in our sample, not all subjects in the entire population, are randomly assigned to either A  = 1 or A  = 0. Because of the presence of random sampling variability, we do not expect that exchangeability will exactly hold in our sample. For example, suppose that 100 subjects are randomly assigned to either heart transplant ( A  = 1) or medical treatment ( A  = 0). Each subject can be classified as good or bad prognosis at the time of randomisation. We say that the groups A  = 0 and A  = 1 are exchangeable if they include exactly the same proportion of subjects with bad prognosis. By chance, it is possible that 17 of the 50 subjects assigned to A  = 1 and 13 of the 50 subjects assigned to A  = 0 had bad prognosis. The two groups are not exactly exchangeable. However, if we could draw many additional 100 person samples from the population and repeat the randomised experiment in each of these samples (or, equivalently, if we could increase the size of our original sample), then the imbalances between the groups A  = 1 and A  = 0 would be increasingly attenuated. Under this conceptualisation, the sample proportion P̂r[ Y  = 1| A  =  a ] is a consistent estimator of P̂r[ Y a  = 1], and P̂r[ Y a  = 1] is a consistent estimator of the population proportion Pr[ Y a  = 1] if our sample is a random sample of the population of interest. This is the most realistic conceptualisation.

Under either conceptualisation, standard statistical procedures are needed to test the causal null hypothesis Pr[ Y a  = 1  = 1] = Pr[ Y a  = 0  = 1] by comparing P̂r[ Y  = 1| A  = 1] and P̂r[ Y  = 1| A  = 0], and to compute confidence intervals for the estimated association measures, which are consistent estimators of the effect measures. The availability of the value of only one counterfactual outcome for each subject, regardless of whether all subjects in the population of interest are or are not included the study (and regardless of which conceptualisation is used), is the second reason why statistics is necessary in causal inference.

A2 GENERALISATIONS

A2.1 definition of causal effect.

We defined causal effect of the exposure on the outcome, Pr[ Y a  = 1  = 1]≠Pr[ Y a  = 0  = 1], as a difference between the counterfactual risk of the outcome had everybody in the population of interest been exposed and the counterfactual risk of the outcome had everybody in the population been unexposed. In some cases, however, investigators may be more interested in the causal effect of the exposure in a subset of the population of interest (rather than the effect in the entire population). This causal effect is defined as a contrast of counterfactual risks in that subset of the population of interest.

A common choice is the subset of the population comprised by the subjects that were actually exposed. Thus, we can define the causal effect in the exposed as Pr[ Y a  = 1  = 1| A  = 1]≠Pr[ Y a  = 0  = 1| A  = 1] or, by definition of counterfactual outcome, Pr[ Y  = 1| A  = 1]≠Pr[ Y a  = 0  = 1| A  = 1]. That is, there is a causal effect in the exposed if the risk of the outcome among the exposed subjects in the population of interest does not equal the counterfactual risk of the outcome had the exposed subjects in the population been unexposed. The causal risk difference in the exposed is Pr[ Y  = 1| A  = 1]−Pr[ Y a  = 0  = 1| A  = 1], the causal risk ratio in the exposed is Pr[ Y  = 1| A  = 1]/Pr[ Y a  = 0  = 1| A  = 1], and the causal odds ratio in the exposed is (Pr[ Y  = 1| A  = 1]/Pr[ Y  = 0| A  = 1])/(Pr[ Y a  = 0  = 1| A  = 1]/Pr[ Y a  = 0  = 0| A  = 1]).

The causal effect in the entire population can be computed under the condition that the exposed and the unexposed are exchangeable—that is, Y a ⨿ A for a  = 0 and a  = 1. On the other hand, the causal effect in the exposed can be computed under the weaker condition that the exposed and the unexposed are exchangeable had they been unexposed—that is, Y a ⨿ A for a  = 0 only. Under this weaker exchangeability condition, the risk of the outcome under no exposure is equal for the exposed and the unexposed: Pr[ Y a  = 0  = 1| A  = 1] = Pr[ Y a  = 0  = 1| A  = 0]. By definition of a counterfactual outcome Pr[ Y a  = 0  = 1| A  = 0] = Pr[ Y  = 1| A  = 0]. Therefore, when the exposed and unexposed are exchangeable under a  = 0, Pr[ Y a  = 0  = 1| A  = 1] = Pr[ Y a  = 0  = 1| A  = 0] = Pr[ Y  = 1| A  = 0]. We decided to restrict our discussion to the causal effect in the entire population and not to the causal effect in the exposed because the latter cannot be directly generalised to time varying exposures.

A2.2 Non-dichotomous outcome and exposure

We say that there is a population average causal effect if E[ Y a ]≠E[ Y a ′ ] for any two values a and a ′. In ideal randomised experiments, the expected value E[ Y a ] can be consistently estimated by the average of Y among subjects with A  =  a . For dichotomous outcomes, E[ Y a ] = Pr[ Y a  = 1].

The average causal effect is defined by the contrast of E[ Y a ] and E[ Y a′ ]. When we talk of “the causal effect of heart transplant ( A )” we mean the contrast between “receiving a heart transplant ( a  = 1)” and “not receiving a heart transplant ( a  = 0).” In this case, we may not need to be explicit about the particular contrast because there are only two possible actions, and therefore only one possible contrast. But for non-dichotomous exposure variables A , the particular contrast of interest needs to be specified. For example, “the causal effect of aspirin” is meaningless unless we specify that the contrast of interest is, say, “taking 150 mg of aspirin daily for five years” compared with “not taking aspirin”. Note that this causal effect is well defined even if counterfactual outcomes under interventions other than those involved in the causal contrast of interest are not well defined or even do not exist (for example, “taking 1 kg of aspirin daily for five years”).

The average causal effect, defined as a contrast of means of counterfactual outcomes, is the most commonly used causal effect. However, the causal effect may also be defined by a contrast of, say, medians, variances, or cdfs of counterfactual outcomes. In general, the causal effect can be defined as a contrast of any functional of the distributions of counterfactual outcomes under different exposure values. The causal null hypothesis refers to the particular contrast of functionals (means, medians, variances, cdfs, ...) used to define the causal effect.

A2.3 Non-deterministic counterfactual outcomes

More generally, a non-deterministic definition of counterfactual outcome does not attach some particular value of the random variable Y a to each subject, but rather a statistical distribution Θ Y a (·) of Y a . The deterministic definition of counterfactual outcome implies that the cdf Θ Y a (y) can only take values 0 or 1 for all y . The use of random distributions of Y a (that is, distributions that may vary across subjects) to allow for non-deterministic counterfactual outcomes does not imply any modification in the definition of average causal effect or the methods used to estimate it. To show this, first note that E[ Y a ] = E[ E [ Y a |Θ Y a (·)]]. Therefore, E[ Y a ] =  E [∫ y d Θ Y a ( y )] = ∫ y dE [Θ Y a ( y )] = ∫ y d F Y a ( y ) because F Y a (·) =  E [Θ Y a, i (·)]. The non-deterministic definition of causal effect is a generalisation of the deterministic definition in which Θ Y a (·) is a general cdf that may take values between 0 and 1.

The choice of deterministic compared with non-deterministic counterfactual outcomes has no consequences for the definition of the average causal effect and the point estimation of effect measures based on averages of counterfactual outcomes. However, this choice has implications for the computation of confidence intervals for the effect measures. 9

A3 NO INTERACTION BETWEEN SUBJECTS

An implicit assumption in our definition of individual causal effect is that a subject’s counterfactual outcome under exposure value a does not depend on other subjects’ exposure value. This assumption was labelled “no interaction between units” by Cox, 10 and “stable-unit-treatment-value assumption (SUTVA)” by Rubin. 11 If this assumption does not hold (for example, in studies dealing with contagious diseases or educational programmes), then individual causal effects cannot be identified by using the hypothetical data in table 2. Most methods for causal inference assume that SUTVA holds.

A4 POSSIBLE WORLDS

Some philosophers of science define causal effects using the concept of “possible worlds.” The actual world is the way things actually are. A possible world is a way things might be. Imagine a possible world a where everybody receives exposure value a , and a possible world a ′ where everybody received exposure value a ′. The mean of the outcome is E[ Y a ] in the first possible world and E[ Y a ′ ] in the second one. There is a causal effect if E[ Y a ]≠E[ Y a ′ ] and the worlds a and a ′ are the two worlds closest to the actual world where all subjects receive exposure value a and a ′, respectively.

We introduced the counterfactual Y a as the outcome of a certain subject under a well specified intervention that exposed her to a . Some philosophers prefer to think of the counterfactual Y a as the outcome of the subject in the possible world that is closest to our world and where she was exposed to a . Both definitions are equivalent when the only difference between the closest possible world involved and the actual world is that the intervention of interest took place. The possible worlds’ formulation of counterfactuals replaces the difficult problem of specifying the intervention of interest by the equally difficult problem of describing the closest possible world that is minimally different from the actual world. The two main counterfactual theories based on possible worlds, which differ only in details, have been proposed by Stalnaker 12 and Lewis. 13

Acknowledgments

The author is deeply indebted to James Robins for his contributions to earlier versions of this manuscript.

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Funding: NIH grant KO8-AI-49392

Conflicts of interest: none declared.

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• In this issue Inequalities goes global C Alvarez-Dardet J R Ashton Journal of Epidemiology & Community Health 2004; 58 261-261 Published Online First: 16 Mar 2004.

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