The Central Idea
A causal question asks:
\[ \boxed{ \text{What would the outcome be under treatment compared with the outcome under control?} } \]For one unit \(i\), let
\[ Y_i(1) \]denote the outcome that would occur if the unit received treatment, and let
\[ Y_i(0) \]denote the outcome that would occur if the same unit received control. These are the unit's potential outcomes.
The individual causal effect is the contrast
\[ \tau_i=Y_i(1)-Y_i(0). \]The subtraction is conceptually simple. Observing both quantities is the hard part.
What Is a Counterfactual?
A counterfactual outcome is the outcome that would have occurred under a condition different from the condition actually received.
If unit \(i\) receives treatment, \(Y_i(1)\) is observed and \(Y_i(0)\) is counterfactual. If the unit receives control, \(Y_i(0)\) is observed and \(Y_i(1)\) is counterfactual.
| Assigned Condition | Observed Outcome | Counterfactual Outcome |
|---|---|---|
| Treatment, \(T_i=1\) | \(Y_i(1)\) | \(Y_i(0)\) |
| Control, \(T_i=0\) | \(Y_i(0)\) | \(Y_i(1)\) |
The Observed-Outcome Equation
Let \(T_i=1\) indicate treatment and \(T_i=0\) indicate control. The observed outcome can be written compactly as
\[ Y_i = T_iY_i(1) + (1-T_i)Y_i(0). \]If \(T_i=1\), then
\[ Y_i=Y_i(1). \]If \(T_i=0\), then
\[ Y_i=Y_i(0). \]The equation selects one potential outcome. It does not reveal the other.
The Fundamental Problem of Causal Inference
For one unit at one time, treatment and control are mutually exclusive. A person cannot both take and not take the same medication during the same treatment period. A plot cannot both receive and not receive the fertilizer under identical conditions.
Therefore, the individual effect
\[ Y_i(1)-Y_i(0) \]cannot ordinarily be observed directly. This is the fundamental problem of causal inference.
Causal inference solves a missing-comparison problem. It uses other units, repeated periods, design structure, and assumptions to estimate the outcomes that were not observed.
A Hypothetical Potential-Outcomes Table
Imagine that both potential outcomes were known for six units. This complete table is not normally observable, but it clarifies the causal quantities.
| Unit \(i\) | \(Y_i(0)\) | \(Y_i(1)\) | \(\tau_i=Y_i(1)-Y_i(0)\) |
|---|---|---|---|
| 1 | 50 | 58 | 8 |
| 2 | 60 | 66 | 6 |
| 3 | 55 | 60 | 5 |
| 4 | 70 | 72 | 2 |
| 5 | 65 | 71 | 6 |
| 6 | 75 | 78 | 3 |
The effects differ across units. The total of the six individual effects is
\[ 8+6+5+2+6+3=30, \]so the average treatment effect for these units is
\[ \frac{30}{6}=5. \]In an actual experiment, only one of the two potential-outcome columns would be observed for each row.
The Average Treatment Effect
Because individual effects are not jointly observable, many studies target an average effect. The average treatment effect, or ATE, is
\[ \operatorname{ATE} = E\!\left[Y(1)-Y(0)\right]. \]By linearity of expectation,
\[ \operatorname{ATE} = E[Y(1)]-E[Y(0)]. \]The two means describe the same target population under two alternative treatment policies. The challenge is to estimate both using observed data.
Effects for Different Target Groups
A causal effect must name the population being averaged.
| Estimand | Definition | Target Group |
|---|---|---|
| ATE | \(E[Y(1)-Y(0)]\) | The full target population |
| ATT | \(E[Y(1)-Y(0)\mid T=1]\) | Units that received treatment |
| ATC | \(E[Y(1)-Y(0)\mid T=0]\) | Units that received control |
The ATE, ATT, and ATC can differ when treatment effects vary across units and treatment recipients differ from nonrecipients.
Treatment-Effect Heterogeneity
A treatment may help some units more than others. The effect
\[ \tau_i=Y_i(1)-Y_i(0) \]can vary with baseline characteristics, setting, treatment version, or interacting causes.
An average effect of \(5\) does not mean every unit improves by \(5\). Effects might be \(10\) for one subgroup, \(0\) for another, and negative for a third. Reporting only the average can conceal important benefit and harm patterns.
Subgroup effects should be scientifically motivated and supported by enough information. Searching many subgroups after seeing the results can manufacture unstable patterns.
How Random Assignment Supplies a Counterfactual Comparison
Random assignment makes treatment status independent of the units' potential outcomes in the assignment process:
\[ \bigl(Y(1),Y(0)\bigr)\perp T. \]This means treatment membership does not systematically depend on what the units would experience under treatment or control.
Under valid random assignment,
\[ E[Y(1)\mid T=1] = E[Y(1)\mid T=0] = E[Y(1)], \]and similarly for \(Y(0)\). Therefore, the mean observed in the control group estimates the missing control outcome for the treatment group on average, and the treatment mean estimates the missing treatment outcome for the control group on average.
The Difference in Group Means
In a simple randomized experiment, a natural estimator is
\[ \widehat{\tau} = \overline{Y}_{T=1} - \overline{Y}_{T=0}. \]Under the randomization design, this estimator targets the average effect for the experimental units. Its expectation across valid assignments equals the relevant average treatment effect.
One realized randomized experiment may still have chance imbalance and an estimate above or below the true average effect. Replication and randomization-based uncertainty quantify that sampling or assignment variation.
Why Observational Comparisons Are Harder
In observational data,
\[ E[Y\mid T=1]-E[Y\mid T=0] \]compares different units under different conditions. The observed difference can be decomposed conceptually into a treatment effect and a selection difference.
Treated units may have different untreated potential outcomes from control units:
\[ E[Y(0)\mid T=1] \ne E[Y(0)\mid T=0]. \]That inequality expresses confounding or selection into treatment. The control group may not represent what would have happened to the treated group without treatment.
Exchangeability
Exchangeability means that treatment groups can stand in for one another's missing potential outcomes under the relevant conditions.
Unconditional exchangeability can be written as
\[ \bigl(Y(1),Y(0)\bigr)\perp T. \]In observational studies, researchers may assume conditional exchangeability given baseline covariates \(X\):
\[ \bigl(Y(1),Y(0)\bigr)\perp T\mid X. \]This states that within levels of \(X\), treatment assignment is independent of the potential outcomes. It is sometimes described as no unmeasured confounding, and it cannot generally be verified from observed data alone.
Positivity and Overlap
For every relevant baseline profile \(X=x\), there must be a positive chance of observing each treatment condition:
\[ 0A model can produce numbers outside observed overlap, but those numbers depend on extrapolation rather than supported counterfactual comparison.
Consistency and Well-Defined Treatments
Consistency connects potential outcomes to observed outcomes. If unit \(i\) actually receives treatment \(t\), then
\[ Y_i=Y_i(t). \]This requires the treatment to be defined well enough that “treatment \(t\)” refers to the relevant intervention. If a tutoring program ranges from one brief session to daily individualized instruction, the label may hide multiple treatment versions with different effects.
Dose, timing, delivery, adherence, and co-interventions may need to be included in the treatment definition.
No Interference
The simplest potential-outcomes notation assumes one unit's outcome depends only on its own assigned treatment:
\[ Y_i(t_i). \]Interference occurs when unit \(j\)'s treatment also affects unit \(i\)'s outcome:
\[ Y_i(t_i,t_j). \]Interference is plausible in vaccination, education, communication networks, neighborhoods, markets, and workplaces. A treated person's behavior may affect peers, or one firm's pricing may affect competitors.
When interference exists, treatment policies and exposure patterns must replace the simplest individual-treatment contrast. Cluster randomization can sometimes align the assignment unit with the interference structure.
The Stable Unit Treatment Value Assumption
Two requirements are often grouped under the stable unit treatment value assumption, or SUTVA:
- there are no relevant hidden versions of the treatment; and
- one unit's treatment does not affect another unit's outcome.
SUTVA is not a universal truth. It is an assumption that should be examined in the actual setting.
A Before-and-After Difference Is Not Automatically a Causal Effect
Suppose a unit has outcome \(Y_{\text{before}}\), receives treatment, and later has outcome \(Y_{\text{after}}\). The difference
\[ Y_{\text{after}}-Y_{\text{before}} \]compares two times, not treatment and control at the same time. Maturation, secular trends, learning, regression toward the mean, season, and other events may affect the later outcome.
The counterfactual needed is the same unit's later outcome without treatment, not its earlier observed outcome:
\[ Y_{\text{after}}(1)-Y_{\text{after}}(0). \]Regression Toward the Mean
Units are often selected for treatment because they have extreme outcomes. Some of that extremity may reflect temporary random variation. On later measurement, values tend to be less extreme even without an effective treatment.
If treatment begins after an unusually poor score, a later improvement may reflect both treatment and ordinary regression toward the mean. A contemporaneous control group selected by the same rule helps estimate what would have happened without treatment.
Matching as Counterfactual Construction
Matching pairs treated units with untreated units that have similar measured baseline characteristics. The matched control outcome is used to estimate the treated unit's missing \(Y(0)\).
Good matching requires:
- baseline variables that capture relevant treatment selection and prognosis;
- strong overlap between treatment groups;
- a prespecified distance or matching rule;
- balance checks after matching; and
- an analysis that respects matched sets and remaining uncertainty.
Matching cannot balance variables that were not measured or were measured poorly.
Regression and Standardization
A model can estimate expected potential outcomes under each treatment for the same covariate distribution:
\[ \widehat{E}[Y(1)\mid X=x], \qquad \widehat{E}[Y(0)\mid X=x]. \]Averaging the two predictions over the target population produces standardized outcome means. Their difference estimates an average treatment effect under conditional exchangeability, positivity, consistency, correct modeling, and adequate measurement.
The model fills in missing counterfactuals mathematically. Its credibility comes from the design and assumptions, not from prediction accuracy alone.
Weighting as a Pseudo-Population
If \(e(X)=P(T=1\mid X)\) is a propensity score, inverse-probability weights may take the form
\[ w_i = \frac{T_i}{e(X_i)} + \frac{1-T_i}{1-e(X_i)}. \]These weights create a pseudo-population in which measured baseline covariates are balanced across treatment groups when the model is appropriate.
Extremely large weights signal weak overlap and can make estimates unstable. Weighting does not solve unmeasured confounding or poorly defined treatment.
Prediction Is Not Counterfactual Causation
A prediction model asks what outcome is likely for a unit with observed features. A causal model asks how that outcome would change under an intervention.
A variable can predict \(Y\) strongly without being a useful intervention target. A downstream symptom may predict disease severity but changing the symptom may not change the disease.
\[ P(Y\mid X=x) \]is an observational conditional distribution, while
\[ P\!\left(Y(t)\right) \]concerns an outcome under a specified intervention. They coincide only under causal assumptions.
Counterfactuals for Policy Decisions
A policy question compares outcomes under alternative strategies:
\[ E[Y(\text{policy }A)] - E[Y(\text{policy }B)]. \]The relevant population, implementation conditions, compliance, spillovers, costs, and time horizon must be stated. The effect of offering a program may differ from the effect of receiving it, and both may differ from the effect of mandating it.
Counterfactual notation forces the intervention to be defined rather than leaving “what if?” implicit.
Ethics and Unobservable Alternatives
Some counterfactual comparisons cannot be randomized ethically. Researchers cannot assign harmful exposures, deny clearly effective care without justification, or impose irreversible risks merely to observe both policy conditions.
Observational designs, natural experiments, carefully justified assumptions, mechanistic evidence, and sensitivity analyses may then be necessary. The counterfactual question remains useful even when a randomized experiment is not possible because it clarifies exactly what alternative must be approximated.
Example: A Randomized Review Program
One hundred students are randomly assigned to a new review program or the usual program. The mean final score is \(82\) in the new-program group and \(77\) in the usual-program group.
\[ \widehat{\tau}=82-77=5. \]What Is Observed?
For each student, only the score under the assigned program is observed.
What Is Counterfactual?
For a student assigned to the new program, the score that student would have earned under the usual program is counterfactual, and conversely.
Why Is the Group Comparison Useful?
Random assignment makes the groups comparable in expectation. The usual-program group estimates the missing usual-program outcomes for the new-program group on average.
What Does the Estimate Mean?
The observed difference estimates the average effect of assignment to the new program for the experimental population, subject to implementation, attrition, interference, measurement, and chance uncertainty.
Example: Voluntary Tutoring
Students who voluntarily attend tutoring average \(85\), while nonattendees average \(78\). The difference is \(7\) points.
The causal effect for attendees is
\[ E[Y(1)-Y(0)\mid T=1]. \]Their observed mean supplies \(E[Y(1)\mid T=1]\). The missing term is
\[ E[Y(0)\mid T=1], \]the mean score attendees would have earned without tutoring. The nonattendee mean \(E[Y(0)\mid T=0]\) is an adequate substitute only if the groups are exchangeable after appropriate adjustment.
Motivation, prior performance, schedule, and help-seeking behavior may violate that assumption.
Identification and Estimation
Identification asks whether the causal quantity can be written in terms of the observable data distribution under stated assumptions. Estimation asks how to calculate that quantity from a finite dataset.
For example, under conditional exchangeability, positivity, and consistency,
\[ E[Y(t)] = E_X\!\left[E[Y\mid T=t,X]\right]. \]This formula identifies the mean potential outcome using observed conditional means. A regression, matching, weighting, or stratification procedure may then estimate it.
A highly precise estimator cannot rescue a causal effect that is not identified by the design and assumptions.
Sensitivity to Counterfactual Assumptions
The missing potential outcomes cannot be checked directly. Sensitivity analysis asks how conclusions change when assumptions about them change.
Useful questions include:
- How strong would unmeasured confounding need to be to explain the estimate?
- How would different missing-outcome values affect the result?
- What happens when units with weak overlap are excluded?
- How do alternative treatment definitions change the estimand?
- What level of interference would materially alter the conclusion?
- Do multiple reasonable models produce substantively similar answers?
A Counterfactual Checklist
- Define the unit. For whom or what are potential outcomes defined?
- Define treatment and control. Are dose, timing, delivery, and versions clear?
- Define the outcome. At what time and by what measurement?
- Name the estimand. Individual effect, ATE, ATT, ATC, or policy effect?
- Identify the missing outcome. Which potential outcome is unobserved for each unit?
- Justify exchangeability. Why can one group stand in for another's counterfactual?
- Check positivity. Are both treatment conditions represented for relevant baseline profiles?
- Check consistency. Does the observed treatment match the defined intervention?
- Check interference. Can one unit's treatment affect another unit's outcome?
- Quantify uncertainty. How do chance and assumption uncertainty affect the estimate?
Common Errors
Treating the Control Group as the Same People Untreated
The control group contains different units. It approximates the treatment group's missing outcomes only through design and assumptions.
Calling a Before-and-After Difference the Treatment Effect
Time changes many things. The correct counterfactual is the later outcome without treatment, not simply the earlier observed outcome.
Assuming the Average Effect Applies to Everyone
Individual effects can vary. An average effect summarizes a population and may conceal important heterogeneity.
Ignoring Treatment Versions
A vague label may combine interventions with different doses, timing, quality, or adherence. The potential outcome is not well defined until the condition is.
Confusing Prediction with Intervention
Predicting \(Y\) from \(X\) does not establish what would happen if \(X\) were changed.
Guided Practice
Problem 1
A participant receives treatment, so \(T_i=1\), and the observed outcome is \(Y_i=12\). Which potential outcome is observed, and which is counterfactual?
Show the solution
\(Y_i(1)=12\) is observed. \(Y_i(0)\), the outcome the participant would have had under control, is counterfactual.
Problem 2
For one unit, suppose \(Y_i(1)=18\) and \(Y_i(0)=13\) in a hypothetical complete potential-outcomes table. Compute the individual treatment effect.
Show the solution
\(\tau_i=Y_i(1)-Y_i(0)=18-13=5\).
Problem 3
Four individual effects are \(2\), \(5\), \(-1\), and \(6\). Compute the average treatment effect for the four units.
Show the solution
The average is \[ \frac{2+5-1+6}{4}=\frac{12}{4}=3. \]
Problem 4
In an observational study, every unit with baseline risk above \(80\) receives treatment and every unit below \(80\) receives control. Which causal condition fails?
Show the solution
Positivity or overlap fails by risk level. There is no high-risk control group and no low-risk treatment group, so within-risk counterfactual comparisons are unsupported by the observed data.
Problem 5
A vaccination study assumes one person's vaccination does not affect anyone else's infection risk. Why might this assumption fail?
Show the solution
Vaccination may reduce transmission to others, so one unit's treatment can affect another unit's outcome. This is interference. Potential outcomes may need to depend on both personal vaccination and others' vaccination patterns.
A Final Counterfactual Check
Complete one sentence before claiming an effect:
\[ \boxed{ \text{The observed comparison estimates what would have happened otherwise because }\ldots } \]The rest of the sentence should name the design or assumptions—random assignment, conditional exchangeability, overlap, consistency, no interference, and credible measurement—that make the missing alternative estimable.
Summary
- Potential outcomes \(Y_i(1)\) and \(Y_i(0)\) describe the same unit under alternative treatment conditions.
- The individual effect is \(\tau_i=Y_i(1)-Y_i(0)\), but only one potential outcome is observed for each unit.
- The fundamental problem of causal inference is the inability to observe both potential outcomes for the same unit at the same time.
- Average effects such as the ATE, ATT, and ATC refer to different target groups.
- Random assignment creates exchangeable treatment groups in the assignment process and supports average counterfactual comparison.
- Observational identification requires assumptions such as conditional exchangeability, positivity, consistency, and appropriate handling of interference.
- Matching, regression, standardization, and weighting estimate missing counterfactual outcomes under design and modeling assumptions.
Next Step
Counterfactual reasoning clarifies the causal quantity being estimated. The next lesson examines internal and external validity: whether a study estimates that quantity credibly for its own units and whether the result transports to other people, places, treatments, and times.