One child, two final scores
A school wants to know whether an enriched reading programme improves attainment. One group receives the programme; another continues with ordinary lessons. At term’s end, the enriched group scores four points higher. The arithmetic is sound. The causal conclusion is not yet earned. The groups might have differed before teaching began, their teachers might have selected pupils differently, or the programme might genuinely have helped. The observed difference contains all these possibilities at once.
Donald Rubin’s 1974 paper begins by refusing to let a group comparison define the causal question. Consider one particular child, a specified starting time and a specified measurement time. If the child enters the enriched programme, imagine the reading score at measurement. Call it y(E). If that same child instead enters the control programme at the same starting time, imagine y(C). The causal effect for this trial is y(E) − y(C). A score of 38 under enrichment and 34 under control gives an individual effect of four items.
This definition is modest and radical. It does not say that the child has an enduring, context-free response. It fixes a unit, two mutually exclusive treatments and two times. It also separates the thing sought from the statistic observed. The group difference may estimate an average of individual contrasts, but it is not itself the definition of causation. That distinction disciplines every later step.
The obstacle arrives immediately. At the starting time the child receives E or C, never both. At measurement, one potential score becomes visible while the other remains counterfactual. Repeating the programme later does not recover the lost value because the child has aged, learned and perhaps carried effects from the first treatment. The missing outcome is not a clerical blank that more measurement can always fill. It belongs to a mutually exclusive course of events.
Thought experiment 1 · The sealed duplicate timetable
Setup. A school prints two timetables for the same pupil and seals one before term starts. The visible timetable assigns enrichment; the sealed one assigns ordinary teaching. Single change. Imagine opening the sealed timetable after observing the enriched score. Predict whether its printed assignment reveals the control score. It does not: the alternative treatment was specified, but its outcome never occurred. If you think a later control term recovers it, you have assumed away ageing and carry-over. The case exposes the missing comparison; it cannot identify the missing value.
Worked example 1 · A four-point effect that cannot be measured directly
For pupil A, set y(E)=38 and y(C)=34, so the individual effect is 4. If A receives E, 38 is observed and 34 is missing. A control pupil B scores 34, but substituting B’s score for A’s y(C) assumes that A and B would respond identically to control. Matching can make that assumption more credible; randomisation can justify an average estimator. Neither turns B into A’s unrealised future.
The trial is a unit plus time
Rubin calls a trial a unit together with a treatment-initiation time t₁ and an outcome-measurement time t₂, with t₁<t₂. This time index matters. “Aspirin versus water” is incomplete without saying when it is taken and when pain is assessed. “Enriched reading versus regular reading” is incomplete without fixing programme duration and test time. A treatment effect can change with delay even when the unit and treatment labels remain constant.
The two treatments must also be exclusive. If E means C plus an extra action, receiving both means receiving E. If E and C are alternatives, combining them creates a third treatment rather than a simultaneous observation of the first two. This prevents a verbal trick from dissolving the counterfactual problem. A trial must have well-defined alternatives before its effect can be defined.
Now index M trials by j. Each has two potential outcomes, yⱼ(E) and yⱼ(C), and an individual effect τⱼ=yⱼ(E)−yⱼ(C). Rubin uses their arithmetic mean as a “typical” causal effect. He notes that a median or trimmed mean might sometimes deserve that label instead. The average is analytically convenient, but it can be dominated by a single large response. Choosing the estimand is therefore a substantive decision, not an automatic consequence of having data.
The expression is finite-population and concrete. It asks for the average contrast among the trials under study. It does not yet invoke a probability distribution for people or outcomes. Probability enters when treatments are assigned, trials are sampled, or uncertainty is otherwise modelled. Keeping the fixed potential outcomes separate from the random assignment is one of the paper’s cleanest moves.
Thought experiment 2 · Move only the measurement time
Setup. Treatment E gives rapid relief that fades after six hours; C acts slowly but lasts all day. Single change. Keep the person and treatments fixed, but move t₂ from two hours to twelve. Predict the sign of y(E)−y(C). It may reverse. Calling one treatment “better” without a time is therefore under-specified. A stable answer commits you to persistence or parallel response curves. This probe clarifies Rubin’s trial definition; it does not tell us either curve.
Worked example 2 · The average can hide response types
Four constructed trials have effects +6, +4, 0 and −2, giving an average effect of +2. The same average arises from +2 for every trial. A policy based on the mean treats these populations alike, although the first contains one harmed unit and considerable heterogeneity. Rubin’s estimand answers an average question. It does not identify the distribution of effects from ordinary parallel-group observations.
The missing half is structured, not blank
Let Wⱼ equal one when trial j receives E and zero when it receives C. The observed outcome is Yⱼᵒᵇˢ=Wⱼyⱼ(E)+(1−Wⱼ)yⱼ(C). This compact equation says that assignment acts like a shutter. It selects one fixed potential outcome for observation. It does not manufacture the outcome, and it does not reveal the other.
Because every row lacks one entry, individual effects are unavailable without further structure. A constant-effect assumption could infer the missing value once the constant were known. A predictive model could impute it. A crossover design might supply evidence if carry-over and time trends were negligible. Each route adds assumptions. The central discipline is to write those assumptions where the missing comparison sits, rather than smuggle them into an apparently descriptive regression.
Paul Holland later named this the fundamental problem of causal inference. The phrase is useful, but the 1974 paper already states the operative point: one cannot return to treatment time and expose the same trial to the alternative. Rubin’s contribution is not the vague observation that counterfactuals are hard. It is the pairing of a precise estimand with assignment-based properties that can be derived despite the missing half.
Evidence boundary
The notation alone does not identify causal effects. It tells us which quantities a causal claim concerns and which entries are missing. Identification comes from design, assumptions or both. Estimation adds a procedure; uncertainty adds a probability basis. Those are separate layers.
A known lottery creates a reference set
Take 2N trials, assign N to E and N to C, and calculate the difference between the two observed group means. If the allocation is completely random, each subset of N treated trials is equally likely. The collection of all permitted allocations is the randomisation set. With four trials and two treated places, it has six members. With matched pairs randomised internally, it has 2ᴺ members. The design, not a fitted outcome distribution, supplies the probability space.
For any trial j, complete random assignment puts it in E for half the allocations and C for half. When treated, its contribution to the difference in means is yⱼ(E)/N; when controlled, it contributes −yⱼ(C)/N. Averaging that contribution across the randomisation set gives [yⱼ(E)−yⱼ(C)]/(2N). Summing over all trials yields the finite-sample average causal effect. Thus the familiar difference in means is unbiased over repeated use of the assignment mechanism.
Unbiasedness is a property of the procedure across allocations. It does not say the one realised estimate is close to the estimand. Rubin stresses this limitation. A fair lottery can produce an imbalanced allocation by chance. Knowing that its average error across all possible allocations is zero gives no guarantee that the observed error is small. Precision depends on the spread of the randomisation distribution and can be improved by design or sensible adjustment.
Randomisation offers a second formal benefit. Under a specified hypothesis about every individual effect, the missing potential outcomes can be completed from the observed outcomes. Under the sharp null, for instance, yⱼ(E)=yⱼ(C) for each trial. One can then calculate the chosen statistic for every allocation in the randomisation set and locate the observed statistic in that exact distribution. This supports a probability statement without assuming normally distributed errors.
The hypothesis must be sharp enough to fill every missing entry. An average effect of zero is not enough: positive and negative individual effects could cancel while changing the allocation distribution. This distinction foreshadows the later separation between Fisher’s sharp null and Neyman’s average-effect estimand. Rubin’s paper discusses hypotheses that specify individual effects, including a constant treatment effect, and notes their use in confidence procedures.
The sceptic survives a lucky draw
Rubin does not treat randomisation as a magic eraser. After any realised allocation, a sceptic can find a characteristic that happens to differ between the groups. Perhaps pupils in E have longer hair, earlier birthdays or more active parents. Random assignment gives a response to the systematic version of this challenge: no measured or unmeasured baseline characteristic was permitted to determine treatment, and its imbalance can be assessed against the known lottery. It does not establish that the realised groups are identical.
This point distinguishes an allocation from its assignment mechanism. The same visible split of pupils could arise by drawing names from a hat or by a teacher’s private judgement. The rows in the final dataset would match exactly, yet the evidential status would differ because the counterfactual allocations differ. Under the lottery, every permitted split had a known chance. Under private judgement, probabilities require a model of the judgement process. Causal evidence therefore depends on how the data were produced, not only on the table eventually analysed.
Unbiasedness also has a deliberately narrow scope. It averages over assignments while holding the finite set of potential outcomes fixed. It neither assumes nor proves that those outcomes were randomly sampled from a superpopulation. This is why Rubin can derive the result without a normal error model. The price is that the conclusion initially concerns the enrolled trials. Generalisation needs a second argument, taken up later.
Exact randomisation inference makes the same design dependence visible. Choose a statistic before inspecting the outcomes, posit a sharp causal hypothesis, reconstruct every missing outcome under that hypothesis, and recompute the statistic across the assignment set. The tail proportion is exact relative to the design and hypothesis. Changing the statistic after seeing the realised pattern or forgetting restrictions used in assignment changes the reference distribution. The test’s authority comes from reproducing the actual lottery faithfully.
Worked example 3 · Enumerating all six estimates
Let four trials have y(E)=(8,7,6,5) and y(C)=(4,6,5,5). Their effects are 4,1,1,0, so τ̄=1.5. Assigning E to trials 1 and 2 yields (8+7)/2−(5+5)/2=2.5. Assigning E to 3 and 4 yields (6+5)/2−(4+6)/2=0.5. The other four allocations produce values around them. Averaging all six differences gives exactly 1.5. No single value is forced to equal 1.5.
Thought experiment 3 · Replace the lottery with a hidden rule
Setup. Outcomes and group sizes stay fixed. Single change. Replace the random draw with a head teacher who quietly assigns pupils expected to improve most to E. Predict the mean estimator across repeated cohorts. It now combines treatment response with the selection rule and need not centre on τ̄. Treating the rule “as if random” commits you to an exchangeability claim about all relevant prior causes. The probe diagnoses the source of bias; it cannot measure its size without more information.
Matching removes predictable distance
Rubin next compares randomisation with matching. If two trials would respond identically under E and identically under C, either observed cross-unit contrast equals their average causal effect. Randomisation is then irrelevant to point accuracy because matching has eliminated the cross-unit mismatch. Physical science can approach this ideal with nearly identical specimens and strong mechanistic knowledge. Social studies rarely know enough causes to do so.
With many pairs, assigning opposite treatments within every pair guarantees local balance. Rubin warns that “thoughtless” complete randomisation can put both members of a close pair into the same group, discarding design information. Randomisation should respect structure known before outcomes are observed. Blocking and pairwise assignment combine protection against systematic bias with gains from similarity.
Yet matching never proves identity. A critic can always propose a prior variable that differs between groups and affects the outcome. In a randomised study, the assignment mechanism makes systematic alignment with such variables unlikely in a calculable sense. In a nonrandomised match, credibility rests on the claim that the matched variables capture the important causes of treatment assignment and outcome. More pairs replicate a pattern, but replication does not erase a rule that selects treatment by an unrecorded cause.
Matching also clarifies the difference between balance and equality. Exact balance on a pretest means paired pupils share that recorded number. It does not mean their control potential outcomes are equal, still less that their treatment effects are equal. The pretest matters because a substantive account says it predicts later reading under both programmes. A useless matching variable consumes design freedom without shortening the relevant distance. A harmful post-treatment match can compare units selected by an effect of treatment itself.
Rubin’s hierarchy is practical. If a variable is known to be important before assignment, control it directly through pairing, blocking or restriction. Randomise within that structure to prevent remaining causes from becoming systematic assignment rules. Then analyse in a way that respects the design. This hierarchy is stronger than checking a balance table after treatment labels are fixed because it prevents avoidable imbalance instead of merely reporting it.
Worked example 4 · Thoughtless randomisation
Suppose two high-baseline pupils form one pair and two low-baseline pupils form another. Within-pair assignment gives one E and one C pupil at each baseline. Complete randomisation can place both high pupils in E and both low pupils in C, creating a large baseline imbalance. The complete design remains unbiased across all six allocations, but this realised allocation is noisy. Blocking removes the known source of noise before it occurs.
Adjustment needs a causal reason
A prior variable X is measured before treatment and would have the same value under E or C. A pretest score is a natural example. If X predicts the outcome, adjusting for it can reduce residual variation and improve precision. In observational work, controlling a prior cause of both assignment and outcome can also reduce confounding. The word “can” carries the burden. An adjustment formula does not decide whether X is causally relevant, a harmless predictor, a collider, a consequence of treatment or a proxy for something else.
Rubin makes a sharper warning than many summaries preserve. If the analyst searches among enough prior variables and functional forms, it is possible to obtain almost any desired treatment estimate. Unbiasedness over the randomisation set does not select an intelligent adjustment. One needs a model of how prior variables affect outcomes and should plan the adjustment before seeing the treatment comparison. In the paper’s terms, a variable correlated with observed Y may still be causally irrelevant to the comparison.
For an adjusted statistic in a randomised experiment, exact significance levels remain available by recalculating that statistic under every permitted allocation. The design can therefore validate a chosen analysis procedure without declaring its causal model correct. In nonrandomised data, the same formula lacks this automatic assignment basis. The investigator must defend something like “subjective randomisation”: after conditioning on recorded prior information, treatment assignment is effectively unpredictable with respect to important potential outcomes.
This is neither a licence for casual “as if random” language nor a ban on observational evidence. Rubin argues that carefully controlled nonrandomised studies are necessary when assignment is unethical, impossible or too slow. He places studies on a continuum. Randomised experiments usually control assignment better; observational studies may represent real target populations better. Credibility depends on transparent control of important prior variables, sensitivity to plausible omitted causes and restraint about extrapolation.
Subjective randomisation is an exposed assumption
Imagine being shown two trials that are identical on all information considered causally important before treatment. If you could not predict which received E better than chance, Rubin says there is a meaningful sense in which assignment may be treated as subjectively random. This is a statement about available causal information, not a historical fact about the assignment. It can be weakened by discovering a new variable that predicts both treatment and the potential outcomes.
The proposal is easy to caricature as wishful thinking. Rubin’s actual position is conditional and comparative. Many important questions cannot be randomised. Refusing all observational evidence would force decisions to rely on introspection while potentially informative comparisons sit unused. The responsible alternative is to design the observational study: make treatment groups comparable on prior causes, include several control groups when they expose different biases, pre-specify adjustments, report where overlap fails and explain why hidden selection is or is not plausible.
Even then, a large sample does not convert an assignment assumption into a design fact. More units reduce sampling noise around the observed association. They can expose inconsistent subgroup patterns and support better matching. They cannot balance a hidden cause that deterministically sorted treatment unless its influence is somehow represented or bounded. Precision is about the width of uncertainty conditional on a model; confounding is about whether the model centres on the desired causal quantity.
Rubin also refuses automatic adjustment for every visible imbalance. Suppose age of the oldest living relative differs between groups and correlates with the outcome through family stability. It may be a useful surrogate for an unmeasured cause. In another setting it may be an irrelevant coincidence. The data alone do not settle which story holds. Causal knowledge chooses the adjustment target; the design and analysis then show how much the estimate depends on that choice.
Thought experiment 4 · The outcome-perfect irrelevant variable
Setup. Before treatment, a code is assigned by copying the future outcome from a secure file, but the code neither affects assignment nor the child. Single change. Add this perfectly predictive variable to the adjustment model. Predict whether its predictive power makes it a confounder. It does not. If you adjust solely because prediction is strong, you equate association with a causal role. The case supports Rubin’s demand for causal judgement; its artificial time order does not model an ordinary study.
Worked example 5 · Selection reverses the sign
In a constructed population, every pupil gains two points from E. Pupils with control potential scores 90 and 80 choose C; pupils with scores 50 and 40 choose E. The observed E mean is 47 and C mean is 85, suggesting −38, although every individual effect is +2. The error comes from comparing different baseline potentials. If the selection-driving baseline were measured and adequately controlled, the comparison could recover the positive effect. If it were hidden, sample size would only stabilise the wrong contrast.
Random assignment is not random sampling
The paper carefully separates two inferential journeys. Random assignment supports a causal comparison for the trials actually in the experiment. Random sampling supports generalisation from those trials to a target population. An experiment can be strong on the first and weak on the second: volunteers from one school may be randomly assigned but unrepresentative of future pupils. A representative observational sample can be strong on population coverage yet weak on causal assignment.
If 2N trials are randomly sampled from M target trials and then randomly assigned, averaging over both mechanisms makes the difference in means unbiased for the target-population average effect. In practice, truly random samples are rare. Generalisation rests on “subjective random sampling”, meaning that no important effect modifier systematically separates the study sample from the target. This is an assumption about response differences, not a reward bestowed by random allocation.
The distinction blocks a common overclaim. Internal validity does not automatically transport an effect. External validity does not repair confounding. The two axes should be assessed separately. A study can occupy any quadrant, and improving one may leave the other unchanged.
Worked example 6 · Excellent experiment, narrow target
A tutoring trial randomises 60 volunteers from one selective school and estimates a three-point average effect for those trials. Random assignment supports that local causal estimate. Applying it to all pupils in a national system requires assumptions about prior attainment, teacher capacity, programme fidelity and effect modification. Increasing the trial’s internal sample size narrows randomisation error; it does not make the volunteer pool representative.
Balancing scores, graphs and interference
Rubin’s 1974 language predates several names now attached to the framework. Neyman had used treatment-specific potential yields in agricultural experiments in 1923. Fisher made physical randomisation the basis for exact testing. Rubin extends potential outcomes beyond agricultural design, states the individual missing-comparison problem, connects matching and adjustment to causal estimation, and gives observational studies a disciplined but assumption-dependent place.
Rosenbaum and Rubin’s 1983 propensity-score paper gives one influential successor. If treatment assignment is ignorable after conditioning on observed covariates X, then conditioning on the scalar propensity score e(X)=Pr(W=1|X) can balance their distribution. This solves a dimensionality problem: matches or subclasses need not be formed on every covariate separately. The theorem transfers no protection against an unmeasured confounder, poor overlap or a misspecified treatment model.
Graphical causal models supply a rival notation and a complementary diagnostic. Directed graphs make assumed causal pathways, colliders and interventions visible. Potential outcomes make unit-level treatment contrasts and assignment-based estimands visible. Claims that one language eliminates the other are usually overstated. A graph can encode assumptions under which a potential-outcome contrast is identified; potential outcomes can state the estimand a graph is meant to identify. The serious disagreement concerns which assumptions are easier to express, inspect and defend.
A further boundary is interference. Figure 1 treated each unit’s potential outcome as depending on its own treatment. In a classroom, one pupil’s programme might change peers’ outcomes. Treatment versions might also differ across teachers. Later work packages no interference and well-defined treatment versions into the stable-unit-treatment-value assumption, often called SUTVA. Violating it does not make causality meaningless; it means the potential outcomes need richer indices, perhaps by whole assignment vectors or exposure mappings.
Modern causal inference also distinguishes identification from estimation more sharply. Identification asks whether the target causal quantity is uniquely determined by the distribution of observable data under stated assumptions. Estimation asks how to recover it from a finite sample. Rubin’s 1974 randomised result handles both in a particularly transparent case: the lottery identifies the finite-population average in expectation, and difference in means estimates it. In observational settings, matching or regression may estimate a formula perfectly while the formula fails to identify the intended effect.
That distinction matters for automated analysis. A system can fit treatment models, outcome models and balancing weights, yet none of those computations verifies that the recorded covariates suffice. Good predictive performance on observed outcomes is compatible with poor counterfactual prediction precisely where treatment groups lack overlap. The causal question must therefore remain visible to the operator: which potential-outcome contrast, for which units, under which assignment and transport assumptions?
Thought experiment 5 · One pupil’s treatment reaches another
Setup. Pupil A receives enriched reading and shares new strategies with control pupil B. Single change. Seat A in a different class while keeping B’s own assignment fixed. Predict B’s outcome. If it changes, yB(C) is not a function of B’s treatment alone. Retaining the two-value notation commits you to no relevant spillover. The experiment reveals the index that must expand; it does not estimate the spillover without a design.
| Object | What it makes explicit | Permission earned | Unpaid debt |
|---|---|---|---|
| Rubin 1974 potential outcomes | Trial-specific alternatives, individual contrasts, assignment set | Define effects; derive design-based properties | One outcome missing per trial |
| Random assignment | Known probability over allocations | Unbiased finite-sample comparison; exact tests under sharp hypotheses | No guarantee for one estimate or new populations |
| Propensity score | Conditional treatment probability from observed X | Balance observed covariates if ignorability and overlap hold | Hidden confounding and poor overlap |
| Causal graph | Assumed pathways, interventions, colliders | Identification logic under encoded assumptions | Graph correctness and estimand choice |
| Interference model | Outcomes indexed by others’ assignments or exposure | Spillover estimands under a stated design | Combinatorial exposure and design dependence |
Worked example 7 · Propensity balance with no overlap
Suppose recorded X predicts treatment so strongly that every high-X unit receives E and every low-X unit receives C. Estimated propensity scores cluster near one and zero. Matching on e(X) finds no comparable partners. The scalar has compressed X but cannot invent support. Any effect estimate must extrapolate across the gap, change the target population or admit that the available data do not identify the desired contrast.
Executable randomisation laboratory
The laboratory fixes eight pairs of potential outcomes, then enumerates all 70 allocations with exactly four treated trials. It demonstrates three propositions: the mean difference-in-means across the randomisation set equals the finite-population average effect; one realised allocation may miss it; and selecting the four units with the highest control potential outcomes produces systematic bias. The numbers are synthetic and visible in the script.
How to inspect it. Choose an allocation, change the sharp constant-effect hypothesis if desired, and run. A positive exact test means the three internal invariants hold: 70 allocations exist, their estimator mean equals τ̄ to numerical precision, and systematic high-baseline selection is displaced. Failure would indicate an implementation error. Passing demonstrates the finite example only. It does not prove ignorability, treatment consistency, no interference or transport in real data.
Worked example 8 · Read one laboratory result
The fixed outcomes have heterogeneous effects. The vertical teal line marks their average. Bars show how often each rounded estimator occurs under balanced random assignment. The amber line marks the chosen allocation. Its distance from teal is randomisation error for that draw. The printed “sorted assignment” instead treats the four highest control-potential units; its displacement is selection, constructed with information that a real analyst would not observe in full.
The paper’s place in the canon
Paper 0017 sits in Stage S0, First principles, within the module on probability, Bayesian inference, causality and decision theory. Bayes supplies a language for uncertainty about unknown quantities. Metropolis and Hastings show how a stochastic mechanism can make an otherwise inaccessible distribution empirically tractable. Rubin turns probability towards a different missing object: the unrealised outcome under another treatment.
The closest prerequisite is Neyman’s treatment-specific yields, historically prior but translated into English much later. Fisher supplies randomisation as a physical basis for inference. Rubin’s new capability is a reusable grammar linking causal definition, missing potential outcomes, treatment assignment and finite-population estimation in both experimental and observational settings.
Three next readings sharpen different edges. Rosenbaum and Rubin (1983) show how a propensity score can balance observed covariates under explicit assumptions. Holland (1986) clarifies the statistical framing and popularises the “fundamental problem” label. Pearl’s graphical work makes structural identification and intervention paths visible, offering a complementary language and a serious test of what potential-outcome notation leaves implicit.
What the paper earns
It earns a precise definition of a unit-level treatment effect, an exact account of two formal benefits of random assignment, and a disciplined rationale for carefully controlled observational evidence. It does not earn individual-effect recovery, freedom from chance imbalance, automatic covariate choice, immunity to hidden confounding, or transport to an unrepresented population.
Memory studio
Mechanism spine
Problem one trial has two relevant outcomes but reveals one.
Move define y(E)−y(C), then average across fixed trials.
Bridge use a known assignment set to compare observed groups.
Permission unbiasedness and exact tests under sharp hypotheses.
Limit design does not reveal both futures or guarantee transport.
Four separations
- Estimand versus estimate: τ̄ is the target; E−C is a procedure.
- Bias versus error: a centred procedure can miss on one draw.
- Assignment versus sampling: causation here; transport elsewhere.
- Prediction versus causation: a useful predictor need not be a confounder.
Recall ladder
30 seconds: recover the two potential outcomes and the missing comparison.
Five minutes: derive why each unit contributes half as E and half as C across the randomisation set.
One hour: explain matching, adjusted randomisation inference, subjective randomisation, sampling and later propensity scores.
Teach-back test
Without using “counterfactual”, “ignorability” or “unbiased”, explain why a fair treatment lottery helps even though it cannot show what would have happened to the same person under the other choice.
Answer cue
The lottery prevents a systematic rule from deciding who receives which option. Across all allowed lotteries, each person’s two possible responses enter symmetrically, so the group-comparison procedure centres on the desired average contrast.
Five flash prompts
- What is a trial? A unit plus treatment-initiation and outcome-measurement times.
- What is missing? One treatment-specific outcome for every realised trial.
- What does randomisation supply? A known set and probability distribution of permitted allocations.
- Why can matching help? It removes predictable cross-unit response differences before comparison.
- Why is generalisation separate? Assignment governs treatment comparability; sampling or transport assumptions govern target-population relevance.
Read a causal claim as a design claim
Rubin’s paper leaves a durable reading habit. Start by writing the same unit under specified alternatives. Mark which outcome is observed and which is absent. Name the population over which the contrast is averaged. Then ask what made assignment comparable, what prior causes were controlled, what probability space justifies uncertainty, and why the study units represent the target.
This sequence resists two temptations. The first is to call any adjusted association causal because the regression is elaborate. The second is to dismiss every nonrandomised study because it lacks an ideal lottery. Rubin accepts neither. Randomisation has exact formal virtues and should be used when possible. Observational inference remains necessary, but its credibility must be purchased with design knowledge, causal assumptions, matching, planned adjustment and candid limits.
The deepest contribution is therefore a grammar of restraint. Causation concerns contrasts that reality does not jointly display. A design can make a population contrast estimable without abolishing that absence. Once the reader sees those two facts together, causal evidence becomes easier to audit: every estimate is a bridge, and every bridge has visible supports.