5.1.1A causal question needs two specified worlds

5.1.2Potential outcomes and the observed-outcome identity

Let $D_i\in\{0,1\}$ indicate treatment for unit $i$. In the Neyman–Rubin potential-outcomes framework, $Y_i(1)$ is that unit's outcome under treatment and $Y_i(0)$ its outcome without treatment. Parentheses index the treatment condition; they do not denote multiplication. The individual treatment effect is

The observed outcome obeys the consistency identity

1. Untreated unit. If $D_i=0$, the first weight is zero and the second is one, so $Y_i=Y_i(0)$.
2. Treated unit. If $D_i=1$, the first weight is one and the second is zero, so $Y_i=Y_i(1)$.
3. Missing comparison. Neither case reveals both outcomes for that person. We cannot calculate the person's effect from the observed outcome alone.

This notation also carries assumptions. Treatment must have a sufficiently clear meaning that $Y_i(d)$ is defined. The simple two-outcome model assumes one person's treatment does not change another person's outcome; with spillovers, potential outcomes must also describe others' assignments. Different course intensities, treatment versions or follow-up dates may require a richer definition.

5.1.3ATE, ATT and the population being averaged

Effects can differ between people. Three averages answer different questions:

ATE is the average treatment effect across the specified population. ATT is the average effect of treatment on the treated group; ATU is the average effect on those untreated. Linearity of expectation gives $\mathrm{ATE}=E[Y(1)]-E[Y(0)]$, and the same operation inside the treated group gives $\mathrm{ATT}=E[Y(1)\mid D=1]-E[Y(0)\mid D=1]$.

Both terms of an effect must average over the same people. ATT subtracts the untreated potential outcome of the treated people, not the observed outcome of the control group. The law of iterated expectations also gives

Thus ATE and ATT can differ when treatment effects differ and treatment assignment changes the composition of the groups. A result for current participants is not automatically the effect of treating everyone else.

5.1.4A complete toy population and the missing cells

The following seven-person model supplies both potential outcomes so we can inspect the identification problem. The numbers are invented outcome points, not observed study data. The treatment assignments mirror the structure of the introductory example. Bold cells are observed; the other potential outcome would ordinarily be missing.

1. Average individual effects. Their sum is $34$, giving $\mathrm{ATE}=34/7\approx4.86$ points.
2. Keep the treated group fixed. People 1, 3 and 4 have effects $10,6,4$, so $\mathrm{ATT}=20/3\approx6.67$.
3. Observed comparison. Treated observed outcomes average $130/3\approx43.33$; untreated outcomes average $60$. Their observed difference is $-50/3\approx-16.67$.
4. Interpretation. Treatment benefits these treated people in the model, yet their observed outcomes are lower. Their no-treatment baseline was already much lower than the control group's.

5.1.5Check the target before using a comparison

5.2.1Deriving the selection-bias identity

Define the observed population difference $\Delta=E[Y\mid D=1]-E[Y\mid D=0]$. Assume both treatment groups have positive probability. Consistency turns the first mean into $E[Y(1)\mid D=1]$ and the second into $E[Y(0)\mid D=0]$. Add and subtract the unobserved treated group's no-treatment mean:

The first two terms are ATT. The last two form selection bias, here denoted $B$:

This is an algebraic identity, not an independence assumption. It always describes how the observed mean difference relates to ATT in this two-outcome model. The identification question is what justifies learning about the unobserved mean inside $B$.

5.2.2Reading the sign of selection

Return to the seven-person model. Treated people's no-treatment mean is $110/3$, while the control group's no-treatment mean is $60$. Therefore

A negative observed difference is compatible with a positive treatment effect because selection bias is more negative. If a training programme enrolls people whose earnings prospects are weak, comparing them with all nonparticipants can underestimate its benefit. If a university selects applicants whose earnings prospects were strong already, the same comparison can overestimate its benefit. These are possible selection mechanisms, not deductions from a difference alone.

1. Observed outcomes only: the treated average $130/3\approx43.33$ and the controls $60\text{.}$ The comparison $\Delta=-50/3\approx-16.67$ makes treatment look harmful.
2. This toy model also supplies the treated people’s missing no-treatment outcomes, $20\text{,}$ $40$ and $50\text{.}$ Every one of them gains: $\mathrm{ATT}=(10+6+4)/3=20/3\approx6.67\text{.}$
3. The comparison splits as $\Delta=\mathrm{ATT}+B\text{:}$ $-16.67=6.67+(-23.33)\text{.}$ The selection term $B=110/3-60$ says the treated would have scored lower anyway.
4. A negative observed difference is compatible with a positive effect. Recovering ATT needs evidence about $B\text{,}$ which the observed outcomes alone cannot give.

5.2.3Two earnings comparisons with different selection mechanisms

A university earnings premium

Suppose, as a lecture illustration, graduates of university O earn $£4{,}000$ more than graduates of university X at a stated follow-up date. That observed difference equals ATT plus selection bias for the population and treatment definition used. If the O group would have earned more even at X, $B>0$, so $\mathrm{ATT}<£4{,}000$. For example, $B=£3{,}000$ would imply ATT $£1{,}000$. The observed premium alone does not establish either amount or justify a causal claim about tuition.

A negative training comparison

Use the illustrative difference $-£8.80$ per week from the training example. If participant selection contributes $-£12$, the implied ATT is $-8.80-(-12)=£3.20$ per week. The same negative comparison would suggest harm if selection were zero. These numbers illustrate the decomposition; they are not a verified evaluation of a historical programme.

Selection on gains and selection on baseline outcomes need distinction. People may choose treatment because they expect a large benefit, producing ATT different from ATE. The bias term in this particular identity concerns the untreated baseline $Y(0)$. A claim about selection on gains alone does not determine its sign.

5.2.4Recover an effect only when the bias term is justified

5.3.1Randomize assignment, not the outcome

Random assignment makes the assignment mechanism independent of potential outcomes. In a population model with treatment assigned with the same positive probability to every unit, write

Read the symbol as “D is independent of the pair of potential outcomes.” This does not say observed $Y$ is independent of $D$. A treatment effect is precisely a way in which assignment can change the observed outcome.

1. Independence for the untreated world. $E[Y(0)\mid D=1]=E[Y(0)\mid D=0]=E[Y(0)]$.
2. Selection term. These equal means make $B=0$, so the observed population comparison equals ATT.
3. Independence for both worlds. Also $E[Y(1)\mid D=1]=E[Y(1)]$. Therefore the same comparison equals ATE; in this population model ATT equals ATE.

The mechanism supports comparisons of both observed and unobserved baseline characteristics in expectation. It does not require measuring every cause of the outcome to remove assignment selection.

5.3.2Balanced in expectation is not exactly balanced in every allocation

A realised experiment contains finitely many people. Some random allocations put more high-baseline units in treatment than in control. In a finite-population experiment with a fixed number assigned to each group, the difference in observed means is unbiased for the finite-population ATE over the assignment distribution. It is not necessarily equal to that ATE in the allocation actually obtained.

For the seven-person model, fix three treated units and enumerate the $\binom73=35$ possible complete random assignments. Each allocation has probability $1/35$. Potential outcomes stay fixed while the observed cells and group means change. Averaging the difference over all allocations recovers $34/7$; a particular allocation can be far from it. With heterogeneous effects, the ATT among the people actually assigned can also differ from the full-population ATE.

After the design establishes a causal target, inference quantifies chance variation. The interval chapters explain how standard errors depend on design; matched, clustered or stratified randomization can require methods beyond an independent two-group formula.

5.3.3An offer and treatment received are different variables

Let $Z$ be randomized assignment to an offer and $D$ actual treatment received. Non-compliance means some people offered treatment do not take it. Contamination means some assigned to control obtain it. Both can make received treatment depend on characteristics or potential outcomes.

Comparing people by their received treatment generally forfeits the randomization argument. Comparing them by their randomized offer preserves an intention-to-treat contrast, provided outcomes are observed appropriately and the assignment design is maintained:

ITT answers the effect of assigning the offer, including take-up under that policy. It is not automatically the effect of receipt. If the offer changes receipt and has no other outcome pathway, stronger assumptions can identify a treatment effect for compliers. The instrumental-variable chapter explains why that effect can be local rather than the ATE.

Differential attrition is another issue: randomized assignment does not ensure that the observed-outcome subset remains comparable. Report take-up and missing outcomes by original assignment group, and explain how each alters the target or identification argument.

5.3.4State what was randomized

5.4.1Internal and external validity ask different questions

Internal validity concerns whether the study credibly identifies its stated effect for the units and treatment actually studied. External validity concerns whether that result transports to another target population, setting, implementation or time horizon. Good random assignment can support the first without establishing the second.

Participants may change behaviour because they are being observed, sometimes called a Hawthorne effect. Expectations about receiving treatment can also affect outcomes, often discussed as placebo effects. Neither label establishes a universal effect size. Define the comparison: if observation and expectations differ between arms, a contrast may include these components; blinding or an appropriate control can help separate them.

A short study may observe an immediate surrogate rather than the long-term outcome relevant to policy. A biomarker, exam score or short-term employment status is not automatically a complete substitute for later health, learning or earnings. Repeating studies across settings can help identify which circumstances matter, but does not mechanically guarantee transport.

5.4.2Changing scale can change the intervention

The simple potential outcome $Y_i(d)$ holds others' assignments implicit. If one person's treatment affects neighbours or coworkers, specify outcomes such as $Y_i(d_i,\mathbf d_{-i})$. A small programme and a universal policy then generate different surrounding assignments. Direct effects on recipients and indirect effects on others are different targets.

For a hypothetical preventive intervention, protecting one participant and reducing exposure among untreated neighbours would be two distinct pathways. For a training programme, reallocating a few jobs can have a different effect from increasing everyone's skills. These illustrations explain why effects at trial scale need not equal effects after economy-wide or community-wide adoption; they do not supply medical efficacy claims or policy estimates.

5.4.3External events need an identification argument

When researchers cannot randomize, external events or institutions can create useful treatment variation. A natural experiment uses variation arising outside researcher control; a quasi-experimental design attempts to build a credible comparison from a mechanism that resembles random allocation in the relevant respect. The terminology alone does not validate a design.

Consider studying neighbourhood relocation after a storm or landslip. Destruction might induce some households to move. But hazard exposure may vary with location, building quality or poverty, and the disaster can affect income directly through injury, asset loss or disruption. To interpret a relocation contrast, examine baseline comparability, other outcome pathways and who relocates. An event's unpredictability to residents does not by itself make its consequences independent of potential outcomes.

1. Name the source of variation. What changed assignment, eligibility or treatment intensity?
2. State the comparison. Which units would be comparable under the assignment rule?
3. Exclude competing pathways. Could the event affect the outcome other than through the treatment being studied?
4. Define the local target. Which units and margin of treatment change does the design identify?

5.4.4A threshold rule creates a useful design opportunity

Angrist and Lavy's 1999 study used an institutional class-size rule as a source of variation. Under the illustrative rule, a grade's enrolment $n$ is divided into enough classes to keep each at no more than $40$. The predicted average class size is

The ceiling symbol means “round up to the next integer.” At $n=40$, one class has size $40$; at $n=41$, two classes average $20.5$. Enrolment changes smoothly by one pupil while predicted class size jumps. Compare schools near a threshold, with a credible argument about other changes at that cutoff. Actual class sizes need not follow the rule perfectly, so the rule can provide an instrument rather than a perfectly assigned treatment.

The historical study and data periods are described in the authors' working-paper record. The expression here illustrates the mechanism, not a current description of all school policies. A discontinuity is useful only if other outcome determinants do not change discontinuously at the same threshold and units cannot sort in a way that defeats the comparison.

5.4.5Examine the design rather than its label

5.5.1What conditioning is assumed to remove

Suppose we observe pre-treatment covariates $X$, such as prior attainment, age or work history. $X$ may be a vector even when we use a single letter. Conditional independence, also called unconfoundedness in this setting, assumes

Within a fixed covariate group, assignment is independent of the pair of potential outcomes. This says selection on the recorded covariates accounts for the remaining systematic assignment differences relevant to those outcomes. It does not say that potential outcomes are constant within a group, or that adjusting for any long list of variables must make the assumption true.

Write $m_d(x)=E[Y\mid D=d,X=x]$, the observed mean for assignment group $d$ in covariate group $x$. Consistency and conditional independence imply, wherever both assignment groups exist,

The within-group causal contrast is $\tau(x)=m_1(x)-m_0(x)$. To see why, repeat the selection-bias decomposition holding $X=x$ fixed: conditional independence makes the within-group untreated baseline difference zero. It also equates treated and full-group average effects at that value of $x$.

5.5.2ATE and ATT use different covariate weights

Knowing all the within-group effects is not enough to select a population target. For a discrete covariate, the law of iterated expectations gives

ATE uses the whole target population's covariate distribution. ATT uses the covariate distribution of treated people. Equal within-group identification does not make these aggregate averages equal when effects and group composition vary. A simple average over cells would assign equal weight to cells regardless of their population shares.

For a continuous covariate, replace sums by integration against the relevant distribution: $\mathrm{ATE}=\int\tau(x)f_X(x)\,dx$, while ATT uses $f_{X\mid D=1}(x)$. These densities describe the target weights, not a different conditional treatment effect.

A two-cell example

In a hypothetical population, half have $X=0$ and half $X=1$. Treatment probabilities are $0.2$ and $0.8$, respectively. Let $m_0(0)=10$, $m_1(0)=12$, $m_0(1)=20$, $m_1(1)=26$. Assume CIA for this constructed example. Effects are $2$ and $6$.

1. Total treatment probability. $P(D=1)=0.5(0.2)+0.5(0.8)=0.5$.
2. Treated covariate weights. By conditional probability, $P(X=0\mid D=1)=0.1/0.5=0.2$; the other weight is $0.8$.
3. ATE. $0.5(2)+0.5(6)=4$.
4. ATT. $0.2(2)+0.8(6)=5.2$.
5. Raw difference. Treated mean is $0.2(12)+0.8(26)=23.2$; control mean is $0.8(10)+0.2(20)=12$. The difference $11.2$ contains ATT $5.2$ plus baseline selection $6$.

5.5.3Common support is a separate requirement

Define the propensity score $e(x)=P(D=1\mid X=x)$, the treatment probability at a covariate value. For ATE identification by comparing conditional means, require

throughout the target covariate support, apart from sets of probability zero. If all units with a particular covariate profile are treated, no untreated mean at that profile is observed. If all are untreated, the treated mean is missing. A fitted prediction does not turn a missing comparison into an observed one: it adds extrapolation assumptions.

ATT needs an untreated comparison over the covariate profiles present among treated people. One may instead restrict the target to a region of common support, but then the estimand is an effect for that restricted population. Report this change rather than continuing to call the result the unrestricted ATE.

In samples, even positive population overlap may provide few comparable observations. This is an estimation problem layered on top of identification. A model may smooth across nearby values, but smoothness, functional form and uncertainty then matter.

5.5.4Why fine adjustment rapidly produces sparse cells

Consider an explicitly uniform hypothetical dataset of $100$ points in a $k$-dimensional unit cube. A cell with side $h$ in every dimension occupies fraction $h^k$ of the cube. The expected count is therefore $100h^k$, provided the cell lies wholly inside the support.

For five dimensions, obtaining an expected total count of five requires

The cell spans more than half the range of each variable. It still provides only an expected total of five observations, not five in each assignment group. This calculation illustrates the curse of dimensionality under uniformity; it is not a prediction for every real dataset. Nonuniform densities, boundaries and treatment selection can make particular cells more or less populated.

5.5.5An adjusted comparison is only as credible as its adjustment argument

A historical application compares military applicants who enlisted with applicants who did not, using recorded screening characteristics. Angrist's 1998 paper includes a matching/regression strategy as well as an instrumental-variable strategy; see the author's paper record. Here the important identification question is whether unmeasured factors behind the final enlistment decision also predict potential earnings.

For example, persistence or reliable attendance might affect both completion of enlistment and earnings without service. If the covariates do not account for this mechanism, holding recorded variables fixed does not remove the selection problem. Neither the number of controls nor similar observed means directly tests independence involving missing potential outcomes.

Choose covariates using their place in the assignment and outcome mechanism. Relevant pre-treatment confounders can help. Variables caused by treatment can remove part of the effect or introduce selection. Even a pre-treatment variable can be a harmful collider in some causal structures, so timing alone is not a complete rule. The next chapter shows why “control for everything” is not a sound strategy.

5.5.6Check weights, overlap and credibility separately

5.6.1A descriptive pay gap is a defined statistic

The dated ONS 2021 bulletin reports UK median hourly-pay gaps excluding overtime: $7.9\%$ for full-time employee jobs, $-2.7\%$ for part-time jobs and $15.4\%$ overall. These historical figures were provisional. The achieved ASHE sample was about $140{,}000$, smaller than before the pandemic, with greater uncertainty. Full-time meant more than $30$ paid hours weekly, or at least $25$ for teaching professions.

The statistic compares pay across jobs; it is not a matched comparison of people doing the same job. The release also reports larger gaps for older and higher-paid groups. These describe distributions, not a causal effect of a specified intervention. A median gap is computed as the difference in group medians divided by the men's median.

Crucially, a pooled median is not a weighted average of subgroup medians. The law of iterated expectations is a statement about means. Do not use it to reconstruct these published median gaps. Even for means, the male and female subgroup weights can differ, and a ratio of means is not generally an average of subgroup ratios.

5.6.2Use a mean illustration to see the composition mechanism

Retain the lecture's rounded pay numbers as an explicitly hypothetical two-stratum mean model. This example is useful for understanding composition; it is separate from the official median calculation.

Pay is in pounds per hour. Apply each group's own weights:

The aggregate mean gap is

Within full-time jobs it is about $7.90\%$; within part-time jobs it is about $-2.65\%$. The aggregate exceeds both because women have a larger share in the lower-paid stratum. There is no contradiction: different mixture weights define the overall populations. The rounded inputs do not reproduce $15.4\%$, and we do not replace exact arithmetic with that published figure.

5.6.3What Simpson-type reversals reveal

A pooled comparison can be much larger than, smaller than or opposite in sign to every within-group comparison when group composition differs. This is the mechanism commonly discussed under Simpson's paradox. It appears in comparisons of admissions across departments or treatment outcomes across case-severity groups: a group can concentrate in harder-to-enter departments or more difficult cases.

To diagnose the pattern, display the subgroup outcomes and each comparison group's subgroup weights. Do not pick the pooled or adjusted result merely because it is more favourable to a claim. Decide which target and comparison the question requires. A decomposition explains an arithmetic pattern, while a causal interpretation requires an account of why the conditioning variable belongs in the design.

If occupation is partly an outcome of barriers, preferences, past opportunities or the treatment under study, conditioning on occupation can remove a relevant pathway and compare differently selected people. A within-job descriptive gap can be useful for its own stated purpose without identifying the total effect of a broader access intervention.

5.6.4A confounder and an outcome are different control candidates

Arrows express hypothesized causal directions, not estimated correlations. The second diagram contains $D\to W\leftarrow U$, a collider at $W$. Among people who reach a selected occupation, those facing a more restrictive access route may have different underlying characteristics. Conditioning can therefore create a comparison that was absent before selection. These graphs are stated toy mechanisms; deciding the appropriate graph is substantive work.

5.6.5Two potential occupations create four types

Extend the potential-outcomes model with $W(0)$ and $W(1)$, potential occupation indicators under two treatment states; $1$ denotes a professional job. Observed occupation follows

Professional workers observed in state 1 belong to $\{W(1)=1\}$; those in state 0 belong to $\{W(0)=1\}$. These need not be the same types of people. This remains true even under a toy assumption that assignment $D$ is jointly independent of all potential earnings and occupations.

The lecture uses female/male labels to motivate differential access. For a real causal study, a recorded demographic attribute alone does not fully specify an intervention. One might instead define changes in perceived classification, hiring treatment or access rules, specifying the pathways and treatment versions of interest. The two-state model here shows a selection mechanism; it does not estimate a causal effect of sex or establish that any particular access mechanism operates in the population.

5.6.6Equal observed pay within a profession can mask a negative effect

Under the stated joint-independence toy assumption, the observed professional contrast can be written without conditioning further on $D$:

Add and subtract $E[Y(0)\mid W(1)=1]$. This produces a causal contrast for the fixed group that would be professional under state 1, plus a composition difference between the two potential professional groups:

The reference group stays $W(1)=1$ in both terms of $\tau_W$. Calling it an unrestricted ATE would be wrong. Removing $D$ from these conditional means requires joint independence involving earnings and occupation; separate pairwise independence statements are not sufficient in general.

A fully specified counterexample

Imagine the following potential population, with assignment independent of type. Earnings are invented units.

1. Individual effects. Every type has $Y(1)-Y(0)=-15$.
2. Professionals in state 1. Only the first type qualifies, so their observed mean is $85$, and their counterfactual state-0 mean would be $100$.
3. Professionals in state 0. The first two types qualify. Their mean is $[0.5(100)+0.3(60)]/0.8=85$.
4. Observed within-profession gap. It is $85-85=0$, yet $\tau_W=-15$ and $B_W=100-85=15$.

The example establishes logical compatibility: zero observed within-profession difference does not rule out a negative causal contrast when composition changes. It does not establish the direction or size of a real-world bias. A total effect, a direct effect holding occupation fixed and a comparison among always-professional types are different estimands and require different assumptions.

1. Three types of people, with shares $50\%\text{,}$ $30\%$ and $20\%\text{,}$ have earnings under both states. Every type earns $15$ less under $D=1\text{.}$
2. Occupation depends on the state: types A and B are professionals under $D=0\text{,}$ but only type A under $D=1\text{.}$
3. Compare professionals only: $(0.5\cdot100+0.3\cdot60)/0.8=85$ under $D=0$ and $85$ under $D=1\text{.}$ The within-profession gap is $0\text{.}$
4. For the same people, type A, the effect is $\tau_W=85-100=-15\text{.}$ The $D=0$ professionals also include lower-paid type B, so $B_W=100-85=+15\text{.}$ The zero gap is $-15+15\text{:}$ conditioning on a job changes who is compared.

5.6.7Separate descriptive standardization from causal identification

5.7.1Why an instrument changes the treatment comparison

This chapter supplies an additional derivation of local average treatment effects, a topic named in the introductory outline. The mechanism and conditions follow the framework associated with Imbens and Angrist's work. An instrument $Z$ changes the probability of receiving treatment $D$. A randomized offer is a useful example: assignment is known, while receipt may still be chosen.

Define $D(1)$ and $D(0)$, potential receipt under an offer and no offer. Under exclusion, the offer has no effect on the outcome except through receipt, so the outcome under assignment is $Y(D(Z))$. This is a substantive restriction: information, expectations or alternative services caused by the offer could violate it.

In addition to exclusion, use four conditions for the elementary binary-instrument result: joint independence of $Z$ from all potential receipt and outcome variables; positive probabilities of both assignment states; a nonzero effect of assignment on receipt; and monotonicity $D(1)\ge D(0)$. Also require the defined treatment versions, consistency and no interference used in the preceding model.

5.7.2Compliance types and the role of monotonicity

Monotonicity rules out defiers for this instrument and treatment direction. It does not say all people comply, that effects are positive, or that the complier effect equals the population average. Under independence and no defiers, the difference in receipt rates is the population share of compliers:

Always-takers and never-takers keep the same receipt state when the offer changes. Under exclusion, they contribute no outcome change caused by the offer. Compliers switch from $Y(0)$ to $Y(1)$.

5.7.3Deriving the Wald ratio

1. Outcome effect of the offer. Independence identifies the assignment contrast as the expected change in $Y(D(Z))$.
2. Split by compliance type. Under exclusion, only compliers change outcomes when assignment changes; monotonicity removes the oppositely switching type.
3. Weight their effect. The outcome contrast is therefore $\pi_C E[Y(1)-Y(0)\mid C]$.
4. Remove the complier share. Divide by the nonzero receipt contrast $\pi_C$.

Read LATE as “local average treatment effect.” It is local to the people whose receipt changes under this particular instrument. Another offer, eligibility threshold or encouragement may move different people and identify another local average. With heterogeneous effects, LATE, ATE and ATT can all differ.

A numerical offer example

In a hypothetical valid-instrument model, $20\%$ are always-takers, $50\%$ compliers and $30\%$ never-takers. Receipt rises from $0.20$ without the offer to $0.70$ with it. Suppose the outcome assignment difference is $3$ points. The complier effect is $3/(0.70-0.20)=6$ points. Effects for always-takers and never-takers are not recovered from this comparison alone.

1. A randomised offer gives both groups the same mix of types: $20\%$ always-takers, $50\%$ compliers and $30\%$ never-takers.
2. Receipt rises from $0.20$ without the offer to $0.70$ with it. Only compliers switch, so $\Delta_D=0.50$ is the complier share.
3. The offer raises the average outcome by $\Delta_Y=3$ points. If the offer affects outcomes only through receipt, the whole gain comes from the compliers: $0.50\times\mathrm{LATE}=3\text{.}$
4. So $\mathrm{LATE}=\Delta_Y/\Delta_D=3/0.50=6$ points, the effect for compliers. It is not, by itself, the effect for always-takers, never-takers or everyone.

5.7.4A larger receipt effect is not a universal effect

5.7.5Bring identification and inference together

Before reporting a causal estimate, state the intervention, target population, outcome and time; draw or describe the assignment mechanism; name the identifying conditions; check which comparisons have support; and then select inference appropriate to the design. A confidence interval describes estimation uncertainty under its assumptions. It does not include every possible violation of CIA, exclusion, treatment definition or transport.

The course now joins five distinct tasks: probability defines uncertainty; distributions and moments describe measurements; statistics studies sampling variation; time series accounts for temporal dependence; causal inference determines which comparison can answer an intervention question. Use the distinction between an identity, an assumption and a result under conditions whenever a formula seems to promise more than the design provides.