Course Identification: Applied Econometrics, taught by Fabian Krüger (primary lecturer) and Marc-Oliver Pohle (lecturer), with tutorials led by Marc-Oliver Pohle and Sophia Siefert at KIT (Karlsruhe Institute of Technology – The Research University in the Helmholtz Association).
Course Objectives: Focuses on econometrics for causal inference using both experimental data and observational data.
Schedule and Format:
Lectures: Weekly on Fridays, 09:45 – 11:15, Building 05.20, Room 1C-04.
Tutorials: Most weeks on Fridays, 11:30 – 13:00, same room as the lecture. Problem sets are posted on ILIAS approximately one week in advance and cover both econometric theory and R implementation.
Grading and Assessment:
Based on a 90-minute written exam.
Exam Dates: March 3, 2026 (14:00–15:30) and April 24, 2026 (preliminary date, available as a first attempt / offen für Erstschreiber).
Exam Structure: Covers analytical derivations (e.g., deriving formulas, computing estimators in numerical examples) and conceptual questions (e.g., comparing concepts, interpreting R output). Active R coding is not tested directly on the exam.
Main Course References:
Primary textbook: Ding, P. (2024), A First Course in Causal Inference, Chapman & Hall/CRC, Texts in Statistical Science.
Synthetic control reference: Abadie, A., Diamond, A., and Hainmueller, J. (2010), Synthetic Control Methods for Comparative Case Studies: Estimating the Effect of California's Tobacco Control Program, Journal of the American Statistical Association.
Linear Regression and Pearson Correlation
Two Goals of Econometric Analysis:
Prediction: Assessing the status quo or expected outcome given specific characteristics (e.g., "What is the expected rent for a flat, given its size, location, and equipment?").
Causality: Answering counterfactual or "what-if" questions regarding interventions (e.g., "How would the flat's rent change if the flat was newly renovated?").
Bivariate Linear Regression Model:
General non-parametric relationship between random variables X and Y: E(Y∣X)=f(X) or Y=f(X)+ω.
Linear restriction assumes E(Y∣X)=ε+ϑX or Y=ε+ϑX+ω.
The random error term ω is centered (E(ω)=0) and uncorrelated with X (cov(X,ω)=0).
Ordinary Least Squares (OLS) Derivation:
Parameter vector (ε,ϑ) minimizes the expected squared error:
(ε,ϑ)=argmina,bE[(Y−(a+bX))2]
Solving the first-order conditions yields the population OLS coefficients:
ϑ=var(X)cov(X,Y)ε=E(Y)−ϑE(X)
Coefficient Interpretation:
Intercept ε: Baseline expected value of Y when X=0.
Slope ϑ: Modeled linear effect of a one-unit change in X on Y.
Statistical Significance: Under the assumption that ω∼N(0,σ2), the hypothesis H0:ϑ=0 vs H1:ϑ=0 is tested using a t-test. Rejection at a significance level (e.g., 5%) indicates a statistically significant linear relationship.
Slope ϑ expressed via correlation:
ϑ=ϖXYvar(X)var(Y)
ϖXY∈[−1,1], where ϖXY=1 indicates perfect positive linear dependency (Y=cX,c>0), ϖXY=0 indicates no linear association, and ϖXY=−1 indicates perfect negative linear dependency (Y=cX,c<0).
Key Limitation: Pearson correlation is symmetric (ϖXY=ϖYX) and measures mutual co-movement, not directional causality. Because ϑ is a rescaled version of ϖXY, standard simple linear regression reflects correlation rather than causation.
Multiple Linear Regression with Two Regressors:
Model: Y=ε+ϑX+ϱZ+ω.
ϑ represents the modeled effect of X on Ycontrolling forZ (holding Z fixed).
Example: If Y is apartment price, X is size, and Z is condition, ϑ isolates the price increase per unit size for apartments in identical condition.
Sources of Correlation and Non-Causality
Five Mechanisms Generating Correlation Between X and Y:
X has a direct causal effect on Y (X→Y).
Y has a direct causal effect on X (Y→X).
A third variable Z causes both X and Y (X←Z→Y; confounding / omitted variable bias).
Selection bias: Analyzing a non-representative subset of the population with exceptional behavior in X and Y.
X has an indirect causal effect on Y (X→Z→Y).
Empirical Example: Spurious Correlation (Temperature vs Life Expectancy):
Data: X= global average temperature in °C, Y= global average life expectancy in years across n=63 annual observations (1960–2022).
R2=0.8515, Adjusted R2=0.8490, Residual standard error: 2.245 on 61 degrees of freedom.
Causal Fallacy: This does not imply that a 1°C temperature increase causes a 16-year increase in life expectancy. Both variables increase over time due to economic development and technological progress.
Assuming all pzy>0, \text{RD} > 0 \iff \text{RR} > 1 \iff \text{OR} > 1$.\n- **Empirical Estimation**:\n - For niidpairs(Z_1, Y_1), \dots, (Z_n, Y_n),letcellcountsben_{zy} = #{i : Z_i = z, Y_i = y}.\n - Probabilities p_{zy}areestimatedviasamplerelativefrequencies\hat{p}{zy} = \frac{n{zy}}{n}.\n\n# The Yule-Simpson Paradox\n\n- **Definition**: A situation where the aggregate modeled association between ZandYhasanoppositesigncomparedtotheconditionalassociationsbetweenZandYacrossallstrataofathirdcovariateX.\n- **Kidney Stones Empirical Example**:\n - Sample of n = 700patientswithkidneystonestreatedviatwosurgicalproceduresZ:\n - Z = 1: Open surgical procedure.\n - Z = 0: Small puncture procedure (*Minimal Methode*).\n - Outcome Y = 1(success),Y = 0 (failure).\n - Aggregated Data Table:\n - Z = 1:n_{11} = 273,n_{10} = 77(Total350;Successrate273 / 350 = 78.0\%\n - Z = 0:n_{01} = 289,n_{00} = 61(Total350;Successrate289 / 350 = 82.57\%\n - Aggregated Risk Difference:\n \widehat{\text{RD}} = \frac{273}{350} - \frac{289}{350} = 78.0\% - 82.57\% = -4.57\%\n - Unadjusted data indicates that the small puncture procedure (Z=0)issuperiorby4.57\text{ percentage points}.\n - Conditioning on Kidney Stone Size X(X = 1ifdiameter< 2\,\text{cm}[small];X = 0ifdiameter\ge 2\,\text{cm} [large]):\n - Small Stones (X = 1):\n - Z = 1:n_{11} = 81,n_{10} = 6(Total87;Successrate81 / 87 = 93.10\%\n - Z = 0:n_{01} = 234,n_{00} = 36(Total270;Successrate234 / 270 = 86.67\%\n - \widehat{\text{RD}}{|X=1} = \frac{81}{87} - \frac{234}{270} = 93.10\% - 86.67\% = +6.44\%\n - Large Stones (X = 0):\n - Z = 1:n{11} = 192,n_{10} = 71(Total263;Successrate192 / 263 = 73.00\%\n - Z = 0:n_{01} = 55,n_{00} = 25(Total80;Successrate55 / 80 = 68.75\%\n - \widehat{\text{RD}}{|X=0} = \frac{192}{263} - \frac{55}{80} = 73.00\% - 68.75\% = +4.25\%\n - **Mechanism**: The open surgical procedure (Z=1)wasdisproportionatelyassignedtoseverecases(263of350opensurgerieswereonlargestones,75.14\%),pullingdownitsaggregatesuccessrate.Thesmallpunctureprocedure(Z=0)wasmostlyassignedtomildcases(270of350punctureprocedureswereonsmallstones,77.14\%).\n - **Decomposition of Underlying Relationships**:\n - Effect of XonZ:P(Z=1|X=1) - P(Z=1|X=0) = \frac{87}{357} - \frac{263}{343} = 24.37\% - 76.68\% = -52.31\% \approx -53\%\n - Effect of XonYgivenZ=0:P(Y=1|X=1, Z=0) - P(Y=1|X=0, Z=0) = 86.67\% - 68.75\% = +17.92\% \approx 18\%\n - Effect of XonYgivenZ=1:P(Y=1|X=1, Z=1) - P(Y=1|X=0, Z=1) = 93.10\% - 73.00\% = +20.10\% \approx 20\%\n - Because the association between XandZandbetweenXandYislargerthanthedirecteffectofZonY,theindirectnegativeassociationviaXmasksthepositivedirecteffectofZonY.\n- **UC Berkeley Admissions Example (Bickel et al., 1975)**:\n - Aggregated data showed that gender ZhadasignificantassociationwithadmissionstatusY, favoring male applicants.\n - Controlling for department choice X (the 6 largest graduate departments), the direct gender disparity vanished. Female applicants applied disproportionately to departments with low overall admission rates.\n- **Origins and Prevention of Simpson's Paradox**:\n - *Data Limitations*: Systematic baseline differences between treated (Z=1)andcontrol(Z=0) units in observational settings.\n - *Analytical Limitation*: Failing to account for counterfactual potential outcomes for each unit under treatment vs control.\n\n# Experimental versus Observational Data\n\n- **Experimental Data**:\n - The researcher directly controls treatment assignment Z_i and uses explicit randomization (e.g., coin flips) to allocate subjects into treatment and control groups.\n - Defines the benchmark or "gold standard" for causal inference.\n - **Ethical Constraints**:\n - Treatment must not intentionally harm participants.\n - Withholding beneficial treatments from the control group must be ethically defensible.\n - **Practical/Design Constraints**:\n - Requires researcher control over treatment implementation.\n - Requires tracking participants over extended time horizons for long-term outcomes.\n - Requires infrastructure, compliance tracking, and funding.\n- **Observational Data**:\n - Recorded values are outside the researcher's control; treatment status Z is selected by subjects or nature.\n - Sources: Administrative records, census data, social security files (e.g., IAB Nuremberg), surveys, commercial market data, central bank series (e.g., ECB, Bundesbank, FRED).\n - Prone to selection bias, confounding, and non-random compliance.\n\n# The Potential Outcomes Framework (Rubin Causal Model)\n\n- **Notation and Setup**:\n - Experimental units indexed by i = 1, \dots, n.\n - Binary treatment indicator Z_i \in {0, 1}(Z_i = 1fortreatment,Z_i = 0 for control).\n - **Interventions**:\n - *Well-defined*: Clear operational steps (e.g., taking an aspirin vs not taking an aspirin).\n - *Ill-defined*: Causes that cannot be directly manipulated (e.g., Pearl 2018 critique on obesity/BMI, which can only be manipulated indirectly through diet, exercise, or surgery).\n- **Counterfactual Potential Outcomes**:\n - Y_i(1):Potentialoutcomeforunitiundertreatment(Z_i = 1).\n - Y_i(0):Potentialoutcomeforunitiundercontrol(Z_i = 0).\n- **Stable Unit Treatment Value Assumption (SUTVA)**:\n 1. **No Interference**: Unit i′spotentialoutcomesareunaffectedbythetreatmentassignmentsofotherunitsj \neq i(Y_i(z_1, \dots, z_n) = Y_i(z_i)).\n - *Counterexample*: Social network spillovers where an ad shown to a user influences a friend's purchase decision.\n 2. **Consistency**: Treatment is unique and well-defined without hidden variations in treatment intensity.\n - *Counterexample*: Evaluating "college degree" where quality, major, and rigor vary widely across institutions.\n- **Science Table**:\n - An n \times 2arraylisting\left[Y_i(1), Y_i(0)\right]foralli = 1, \dots, n.\n - Fundamental Problem of Causal Inference: For each unit i, only one potential outcome is observable; the other is counterfactual and missing.\n- **Definitions of Causal Effects**:\n - **Individual Causal Effect**: \omega_i = Y_i(1) - Y_i(0).\n - **Average Causal Effect (ACE / ATE)**:\n \omega = \frac{1}{n} \sum{i=1}^n \omega_i = \frac{1}{n} \sum_{i=1}^n Y_i(1) - \frac{1}{n} \sum_{i=1}^n Y_i(0) = \bar{Y}(1) - \bar{Y}(0)\n- **Experimental Unit vs Physical Unit**:\n - A physical unit (a single individual) observed across two different time points represents two distinct experimental units (i_{\text{before}}andi_{\text{after}}$).
Before decision: Yi,before(0)=1, Yi,before(1)=?
After decision: Yi,after(0)=?, Yi,after(1)=0
Replacing missing outcomes with assumed values demonstrates that causal effects can vary across time for the same physical unit.
Non-Existence of the Yule-Simpson Paradox under Potential Outcomes
Mathematical Proof:
Let discrete covariate Xi∈{0,1} partition units into two subgroups.
Subgroup Average Causal Effect for stratum x∈{0,1}:
ωx=∑i=1n1(Xi=x)∑i=1n1(Xi=x)(Yi(1)−Yi(0))
Proportion of units in stratum x: εx=n∑i=1n1(Xi=x).
The overall ACE is a convex linear combination of subgroup ACEs:
ω=ε0ω0+ε1ω1
Implication: If ω0>0 and ω1>0, then ω>0 necessarily holds. Simpson's Paradox cannot occur when analyzing true potential outcomes; it arises solely from confounding in observed associations.
Treatment Assignment Mechanisms and Observed Outcomes
Observation Mechanism:
The observed outcome Yi is linked to potential outcomes via treatment assignment Zi:
Yi=ZiYi(1)+(1−Zi)Yi(0)=Yi(0)+Zi(Yi(1)−Yi(0))=Yi(0)+Ziωi
The missing/counterfactual outcome is:
Yioth=(1−Zi)Yi(1)+ZiYi(0)
Doctor Simulation Example (Treatment Assignment Impact):
Setup: n=1000 patients (500 assigned to Doctor 1, 500 to Doctor 2). Baseline health Y0∼N(0,1). Individual treatment effects τi=−0.5+ηi, where ηi∼N(0,1). Mean true ACE is −0.5 for both doctors (τˉ1:500=−0.4708, τˉ501:1000=−0.5180).
Perfect Doctor (Doctor 1): Assigns treatment Zi=1 if and only if τi>0.
Observed difference in sample means: YˉZ=1−YˉZ=0=+0.6651.
Result: Misleading positive association despite a negative average causal effect.
Clueless Doctor (Doctor 2): Assigns treatment Zi∈{0,1} via independent coin tosses (P(Zi=1)=0.5).
Observed difference in sample means: YˉZ=1−YˉZ=0=−0.5586.
Result: Unbiased estimate close to the true population ACE (−0.50).
Completely Randomized Experiments (CRE)
Definition and Probability Distribution:
Sample size n, fixed number of treated units n1, fixed number of control units n_0 = n - n_1$.\n - Total number of possible treatment assignment vectors: M = \binom{n}{n_1} = \frac{n!}{n_0! n_1!}.\n - A Completely Randomized Experiment (CRE) selects every treatment assignment vector \mathbf{z} \in {0,1}^nsatisfying\sum_{i=1}^n z_i = n_1 with equal probability:\n P(\mathbf{Z} = \mathbf{z}) = \frac{1}{\binom{n}{n_1}}\n - If potential outcomes are viewed as random variables, CRE assumes independence:\n P(\mathbf{Z} = \mathbf{z} | \mathbf{Y}(0), \mathbf{Y}(1)) = \frac{1}{\binom{n}{n_1}}\n- **CRE versus Bernoulli Randomized Experiments (BRE)**:\n - In a BRE, each Z_i \overset{iid}{\sim} \text{Bernoulli}(p),renderingthetotaltreatedcountn_1 \sim \text{Binomial}(n, p) random.\n - Conditioning a BRE on the observed number of treated units n_1 yields a CRE.\n\n# The Fisher Randomization Test (FRT)\n\n- **Setting and Sharp Null Hypothesis**:\n - Fisher's Sharp Null Hypothesis: H_0^F: Y_i(1) = Y_i(0)foralli = 1, \dots, n (all individual treatment effects are identically zero).\n - Under H_0^F,bothpotentialoutcomesarefullyknownforallunits(Y_i(1) = Y_i(0) = Y_i).\n- **Test Statistic**:\n - Difference-in-means statistic: \hat{\omega}(\mathbf{Z}, \mathbf{Y}) = \hat{\bar{Y}}(1) - \hat{\bar{Y}}(0), where:\n \hat{\bar{Y}}(1) = \frac{1}{n_1} \sum_{i: Z_i = 1} Y_i = \frac{1}{n_1} \sum_{i=1}^n Z_i Y_i\n \hat{\bar{Y}}(0) = \frac{1}{n_0} \sum_{i: Z_i = 0} Y_i = \frac{1}{n_0} \sum_{i=1}^n (1 - Z_i) Y_i\n- **p-Value Formulas**:\n - Two-sided exact p-value:\n p_{\text{FRT}} = \frac{1}{M} \sum_{m=1}^M \mathbf{1}\left(|\hat{\omega}(\mathbf{z}m, \mathbf{Y})| \ge |\hat{\omega}(\mathbf{z}, \mathbf{Y})|\right)\n - One-sided exact p-value (testing for positive effect):\n p{\text{FRT}} = \frac{1}{M} \sum_{m=1}^M \mathbf{1}\left(\hat{\omega}(\mathbf{z}m, \mathbf{Y}) \ge \hat{\omega}(\mathbf{z}, \mathbf{Y})\right)\n- **Small Numerical Example (Job Training Subset, n=5, n_1=3, M=10)**:\n - Units earnings: 2484.55, 12558.00, 743.67, 0.00, 275.57.Truetreatmentvector:(1, 1, 1, 0, 0).\n - Observed difference-in-means: \hat{\omega} = 5124.289\n - Permutation difference-in-means distribution across all 10 allocations:\n 1. (1,1,1,0,0) \rightarrow 5124.289 (True assignment)\n 2. (1,1,0,1,0) \rightarrow 4504.567\n 3. (1,1,0,0,1) \rightarrow 4734.205\n 4. (1,0,1,1,0) \rightarrow -5340.711\n 5. (1,0,1,0,1) \rightarrow -5111.072\n 6. (1,0,0,1,1) \rightarrow -5730.795\n 7. (0,1,1,1,0) \rightarrow 3053.831\n 8. (0,1,1,0,1) \rightarrow 3283.469\n 9. (0,1,0,1,1) \rightarrow 2663.747\n 10. (0,0,1,1,1) \rightarrow -7181.531\n - Results: Two-sided p = 4 / 10 = 0.40;One−sidedp = 1 / 10 = 0.10.CannotrejectH_0^F due to small sample size.\n- **Full Sample Monte Carlo Approximation (n=445, n_1=185)**:\n - Exact M = \binom{445}{185}iscomputationallyinfeasible.UsingN{MC} = 10,000 random permutations:\n - Observed true difference-in-means: \hat{\omega} = 1794.34\n - Monte Carlo p-values: Two-sided p = 0.0042;One−sidedp = 0.0023.\n- **Asymptotic Normal Approximation**:\n - Under H_0^F,\frac{\hat{\omega}(\mathbf{Z}, \mathbf{Y})}{\sqrt{\frac{n}{n_0 n_1} s^2}} \xrightarrow{d} N(0, 1),wheres^2 = \frac{1}{n-1} \sum_{i=1}^n (Y_i - \bar{Y})^2\n - Approximate one-sided p-value:\n p_{\text{FRT}} \approx 1 - \Phi\left( \frac{\hat{\omega}(\mathbf{z}, \mathbf{Y})}{\sqrt{\frac{n}{n_0 n_1} s^2}} \right)\n - Job training asymptotic p-value: 0.002453245.\n- **Extensions**:\n - Generalized null hypothesis H_0(\boldsymbol{\omega}): Y_i(1) - Y_i(0) = \varepsilon_iforavectorofeffects\boldsymbol{\omega} = (\varepsilon_1, \dots, \varepsilon_n).\n\n# Estimation of the Average Causal Effect (ACE)\n\n- **Setting**: CRE with fixed potential outcomes Y_i(1), Y_i(0)orconditionedonpotentialoutcomes.Randomnessstemsentirelyfromtreatmentassignmentvector\mathbf{Z}.\n- **Difference-in-Means Estimator**:\n \hat{\omega} = \hat{\bar{Y}}(1) - \hat{\bar{Y}}(0) = \frac{1}{n_1} \sum_{i=1}^n Z_i Y_i - \frac{1}{n_0} \sum_{i=1}^n (1 - Z_i) Y_i\n- **Proof of Unbiasedness**:\n - Since E[Z_i] = \frac{n_1}{n}andE[1 - Z_i] = \frac{n_0}{n}:\n E[\hat{\omega}] = E\left[ \frac{1}{n_1} \sum_{i=1}^n Z_i Y_i(1) - \frac{1}{n_0} \sum_{i=1}^n (1 - Z_i) Y_i(0) \right]\n E[\hat{\omega}] = \frac{1}{n_1} \sum_{i=1}^n \frac{n_1}{n} Y_i(1) - \frac{1}{n_0} \sum_{i=1}^n \frac{n_0}{n} Y_i(0) = \bar{Y}(1) - \bar{Y}(0) = \omega\n\n# Variance of the Difference-in-Means Estimator\n\n- **Population Potential Outcome Variances and Covariances**:\n S^2(1) = \frac{1}{n-1} \sum_{i=1}^n (Y_i(1) - \bar{Y}(1))^2\n S^2(0) = \frac{1}{n-1} \sum_{i=1}^n (Y_i(0) - \bar{Y}(0))^2\n S(1, 0) = \frac{1}{n-1} \sum_{i=1}^n (Y_i(1) - \bar{Y}(1))(Y_i(0) - \bar{Y}(0))\n S^2(\omega) = \frac{1}{n-1} \sum_{i=1}^n (\omega_i - \omega)^2\n- **Algebraic Identity**:\n 2 S(1,0) = S^2(1) + S^2(0) - S^2(\omega)\n- **Exact Variance Formulas**:\n \text{var}(\hat{\omega}) = \frac{1}{n} \left[ \frac{n_0}{n_1} S^2(1) + \frac{n_1}{n_0} S^2(0) + 2 S(1, 0) \right]\n \text{var}(\hat{\omega}) = \frac{S^2(1)}{n_1} + \frac{S^2(0)}{n_0} - \frac{S^2(\omega)}{n}\n- **Properties of Variance**:\n - Larger sample size n lowers variance.\n - Optimal sample allocation ratio: \frac{n_0}{n_1} = \sqrt{\frac{S^2(0)}{S^2(1)}}.\n - Higher variation in individual treatment effects S^2(\omega) *reduces* variance across random treatment assignments.\n- **Supermarket Simulation Example (n=100, n_1=60, n_0=40)**:\n - Baseline Y_0 \sim \text{Exp}(0.1) sorted in decreasing order.\n - **Case 1 (Same Order)**: Y_1 = Y_0 + 10(\omega_i = 10constant).S(1,0) = 89.09,S^2(\omega) = 0.True\text{var}(\hat{\omega}) = 3.725\n - **Case 2 (Opposite Order)**: Y_1sortedinincreasingorder.S(1,0) = -59.91,S^2(\omega)maximal.True\text{var}(\hat{\omega}) = 0.738\n - **Case 3 (Random Order)**: Y_1randomlyshuffled.S(1,0) = 4.00.True\text{var}(\hat{\omega}) = 2.013\n\n# Variance Estimation and Asymptotic Confidence Intervals\n\n- **Sample Variance Estimators**:\n \hat{S}^2(1) = \frac{1}{n_1 - 1} \sum_{i=1}^n Z_i (Y_i - \hat{\bar{Y}}(1))^2\n \hat{S}^2(0) = \frac{1}{n_0 - 1} \sum_{i=1}^n (1 - Z_i) (Y_i - \hat{\bar{Y}}(0))^2\n - Unobserved terms: S(1,0)andS^2(\omega) cannot be identified from observed data because no individual has both potential outcomes recorded.\n- **Conservative Variance Estimator**:\n \hat{V} = \frac{\hat{S}^2(1)}{n_1} + \frac{\hat{S}^2(0)}{n_0}\n- **Expectation and Bias of Variance Estimator**:\n E[\hat{V}] - \text{var}(\hat{\omega}) = \frac{S^2(\omega)}{n} \ge 0\n - \hat{V}isunbiasediftreatmenteffectsareconstant(S^2(\omega) = 0); otherwise, it overestimates the true variance on average (conservative estimator).\n - Simulation average estimated variance \bar{\hat{V}} across 100,000 iterations:\n - Same order: Estimated 3.711(True3.725\n - Opposite order: Estimated 3.709(True0.738\n - Random order: Estimated 3.710(True2.013\n- **Asymptotic Distribution and Confidence Intervals**:\n - Under regularity conditions, \frac{\hat{\omega} - \omega}{\sqrt{\text{var}(\hat{\omega})}} \xrightarrow{d} N(0, 1).\n - Approximate (1 - \alpha)confidenceintervalforACE\omega:\n \left[ \hat{\omega} - z_{1 - \alpha/2} \sqrt{\hat{V}}, \; \hat{\omega} + z_{1 - \alpha/2} \sqrt{\hat{V}} \right]\n - Simulation empirical coverage for nominal 95\% CI:\n - Same order: 0.946\n - Opposite order: 1.000\n - Random order: 0.990\n- **Hypothesis Test for Weak Null (H_0^W: \omega = 0)**:\n - Reject H_0^Wif0isoutsidethe(1-\alpha) confidence interval.\n - Overestimating variance produces wider CIs, leading to conservative decision-making (lower risk of false positives, but reduced test power).\n\n# Stratification and Stratified Randomized Experiments (SRE)\n\n- **Notation and Framework**:\n - Discrete covariate X_i \in {1, \dots, K}.\n - Subgroup of units with X_i = kisthek\text{-th} stratum.\n - Stratum size: n^{[k]} = #{i : X_i = k};Stratumproportion:\omega^{[k]} = n^{[k]} / n\n - Stratum treatment/control counts: n_1^{[k]} = #{i : X_i = k, Z_i = 1},n_0^{[k]} = #{i : X_i = k, Z_i = 0}.\n- **Limitations of Unstratified CRE**:\n 1. Risk of zero cell counts (n_1^{[k]} = 0orn_0^{[k]} = 0) in one or more strata.\n 2. Imbalance in stratum propensity scores e^{[k]} = n_1^{[k]} / n^{[k]}relativetooverallsampleratioe = n_1 / n$.
Definition of Stratified Randomized Experiments (SRE):
An SRE fixes n1[k] and n0[k] for every stratum k=1,…,K and independently conducts a CRE within each stratum.
Total possible assignments in SRE: MS=∏k=1K(n1[k]n[k])<(n1n).