Investigate a virtual garden. Change who receives an assignment card, uncover a hidden starting difference, run fair trials and discover why a pattern alone cannot settle what caused it.
Enable JavaScript to change the conditions and run the interactive experiment.
Who already received an assignment can differ from who would receive it after a fair shuffle. A causal explanation needs a defensible account of assignment and response; a chart alone does not supply that account.
Two response rulebooks have exactly the same observed W/Y population table. Will more W/Y observations alone tell you which causal effect is right?
Precision about the same observational distribution does not choose between the two mechanisms. Additional measurements, assumptions or a suitable intervention are needed.
In the opening recipe, 30 of 50 baseline-only plots meet a target, compared with 25 of 50 extra-water plots. Those are exact constructed proportions. Decide what the chart establishes before revealing two different response stories.
Open the garden. W0 means baseline care; W1 means an extra-watering assignment. The card is a variable you can change. Each bed keeps its own stored baseline category and response digit when you change assignment.
The default existing policy gives extra-water cards to drier plots more often. Those plots also have a harder baseline. Open the soil layer without redrawing the city. This common cause can make a beneficial rule look harmful in the pooled comparison.
Shuffle equal numbers of W0 and W1 cards independently of dryness. The baseline-to-assignment link is removed. Dryness still affects success, and the stipulated response effect still operates.
Showing only plots that already have W1 retains a selected subset. Setting every plot to W1 retains the whole original cohort and replaces assignment. Compare the row counts and baseline composition side by side.
Split the comparison into dry and less-dry categories, then average each arm’s category rates using the same 50/50 target mix. An empty sample cell has no rate; this calculation stays unavailable rather than guessing a value.
Generate fresh cities and independently shuffle their assignments. Small estimates vary even when the model effect is known. Keep all repetitions, compare them with the exact sampling distribution, and distinguish sampling more plots from running more repetitions.
For binary W and Y, the workbench can calculate their correlation and the difference between success rates in the two observed arms. Neither summary alone specifies the effect of replacing an assignment mechanism. A zero-variance variable makes correlation undefined.
C marks baseline dry-soil category, W marks the assignment, and Y marks a single binary endpoint. Independent population digits RC, RW and RY are uniform on 0 through 9. In A, C=1[RC<5], W=1[RW<5+k(2C−1)], and Y=1[RY<7−5C+tW]. These are authored mathematical rules, not measured plant biology.
A permits t=0,1,2 and k=0,1,2,3,4. The within-category benefit is t/10; k controls how strongly the existing policy favors dry plots. Assignment probabilities remain between 0.1 and 0.9, so both assignments are possible in both categories in the population.
With t=2,k=3, the extra-water population is 80% dry while the baseline-only population is 20% dry. Both within-category intervention differences are +20 percentage points, yet observed rates are 50% versus 60%. This reversal is related to Simpson’s paradox; the causal graph determines which comparison answers the intervention question.
Rulebook B retains the default assignment policy but uses Y=1[RY<6−W], with no direct C-to-Y effect. Both worlds have joint probabilities W0Y0=.20, W0Y1=.30, W1Y0=.25, W1Y1=.25. A has intervention risks .45 and .65; B has .60 and .50. These are equal population observational laws, not a claim that independent finite samples have identical counts.
More observations of only W and Y estimate their common distribution more precisely without selecting between A and B. Measuring the baseline variable or performing the stated intervention can distinguish these particular worlds in principle. This does not mean observation is useless: appropriate assumptions, measured variables and study design can support causal identification.
P(Y|W=1) refers to the existing W1 group. P(Y|do(W=1)) replaces the assignment equation and keeps the full population’s background distribution. The simulator implements the latter by setting W while retaining each stored C and RY. It does not manipulate Y directly to force a preferred answer.
In default A, C causes both W and Y, creating a back-door path. Standardizing category-specific means to a common 50/50 city composition recovers the intervention contrast at the population level. This depends on the stipulated sufficient baseline variable and positivity. It is not permission to adjust for every variable in an arbitrary dataset.
Positive assignment probability in each category does not guarantee all cells appear in a sample of 20. The default observational cohort has no dry baseline-only plot. Its sample cell mean and cell-mean standardized difference are unavailable. Zero rows are not a 0% success rate.
The balanced shuffle assigns exactly N/2 plots to each arm. In the reproducible default 20-plot city, randomized arms contain 6 dry plots versus 2. That chance imbalance does not prove the randomizer is broken. Outcome comparison must respect the planned allocation and sampling procedure.
Assignment governs which response is observed for each sampled unit. Sampling governs which units enter the study. Random assignment alone does not establish representativeness, transportability, absence of missing outcomes or adherence to the assigned action.
The oracle computes Y(0) and Y(1) using the same unit’s C and RY. This coupling defines individual response types inside the simulator. A real experiment ordinarily observes one outcome under one assignment in the same circumstances. An average effect by itself does not identify each individual’s response.
The known population effect averages over the declared probability law. The finite-cohort oracle averages paired Y(1)−Y(0) over the stored plots. The observed arm-rate difference compares different realized groups. These can differ in a finite sample without any calculation being wrong.
At t=0 in A, every unit’s paired outcomes agree, so both population and finite-cohort causal effects are zero. Different units still fall into the two randomized arms; a realized comparison can be nonzero. Under the confounded existing policy at k=3, the population observational contrast remains −30 percentage points.
Under default A, fresh randomized arm successes are independent Binomial(n,.65) and Binomial(n,.45), where n=N/2. Their difference divided by n has mean .20 and variance .475/n. The chart calculates every possible mass by convolution. The shown central sampling range uses discrete 2.5% and 97.5% quantiles; its actual included mass need not be exactly 95%.
For 20 fresh plots, the standard deviation is about 21.79 percentage points and a zero or negative estimate occurs about 24.35% of the time. At 400 plots, standard deviation falls to about 4.87 points. Those are probabilities under a specified positive-effect model, not p-values or probabilities that the effect is zero.
The 20-card activity contains 9 always-success, 4 helped and 7 never-success cards under default A. Exactly 184,756 balanced assignments are possible. Their mean difference is .20 and probability of a nonpositive difference is about .23107. This differs from the fresh-city value .24353 because the response-type composition is fixed.
The optional Wilson intervals estimate individual binomial arm rates under their sampling assumptions. They are not an interval for the difference, and overlap is not a specified difference test. Approximate 95% confidence describes repeated coverage of a method, not a 95% posterior probability attached to one fixed unknown rate.
The versioned SHA-256/rejection generator uses seed, cohort, unit ID, variable stream and draw index. An independent Fisher–Yates shuffle supplies balanced assignments. Filters and reveal controls leave the data unchanged. Changing sample size rebuilds that size’s allocation; it is not appending plots with all former cards guaranteed unchanged.
Ask what was measured, who received the condition, what preceded it, and which causal assumptions support the conclusion. A careful observational statement can be valuable without pretending to settle the intervention.
Define the outcome and comparison before inspecting results. Record assignment, baseline information, all outcomes and all attempted trials. A randomized comparison still needs appropriate sampling, measurement and operational assumptions.
Check whether an arrow is a declared rule or a conclusion from evidence. The garden helps test causal reasoning; its plant-like appearance contributes no independent biological evidence.
A feature that predicts a label can be a shortcut rather than a cause. A model’s attention weight, classification score and response to a specified intervention answer different questions.
Use the downloadable key to make ten less-dry cards and ten dry cards. Each has a response-digit label 0–9 and covered Y0/Y1 boxes. This fixes nine always-success, four helped and seven never-success cards under the stated rulebook.
Mix ten baseline-only and ten extra-watering labels face down. Give one to each plot card without looking at response boxes. Keep each label in place; do not choose assignments after seeing success.
For a W0 card reveal only Y0; for a W1 card reveal only Y1. Keep the other box covered. A 1 means the synthetic target is met and a 0 means it is not.
Record successes, total cards and dry cards in each arm. Calculate extra-water successes/10 minus baseline successes/10. Keep this exact allocation even if the result surprises you.
After recording the result, uncover both boxes. The whole fixed deck has 9 baseline successes and 13 extra-water successes: an average paired difference of 4/20. Explain why this audit is available for authored response cards but not ordinarily for real units.
Cover the boxes, reshuffle all labels and record five more complete allocations. Keep every result. These are new assignments of the same deck, not fresh city samples. Compare your results with the exact fixed-deck table, then explain the difference.
Can a result be surprising without proving that the randomizer or the known rulebook is wrong?
Use fictional paper cards only. No plant manipulation, personal data, health intervention or powered equipment is needed. The online deck is a reproducible companion; a physical shuffle will normally produce different allocations.
The existing W1 group has a lower observed success rate The chart describes an association. The assignment and response story is additional causal information.
C → W, baseline to assignment Randomization replaces assignment. It does not erase baseline influences on the outcome or change the response rule.
No; filtering selects existing rows, while assignment retains the whole cohort In default A the population W1 subset is 80% dry, while the full population retained by intervention is 50% dry.
No; chance imbalance can occur under a valid balanced allocation Equal numbers of labels do not force equal baseline composition. Keep the outcome and interpret the stated design.
Unavailable There is no denominator. The population rule does not create observations in an empty sample cell.
No; different units can still produce a finite estimate Paired outcomes agree within each unit, but different units enter the two arms. The population expectation and a realized comparison differ.
A sampling probability conditional on that positive-effect model The calculation assumes the stated model and sampling design. It is not a probability a hypothesis is true.
Observed −10 points; intervention +10 points The observational contrast is t/10−k/10, while the intervention contrast is t/10. Shared runoff would violate the separate no-interference assumption rather than merely change this answer.
Pearl’s 1995 primary paper, especially structural interpretation and causal diagrams. The garden coefficients and diagrams are original.
Pearl · Causal diagrams for empirical researchPearl’s 2009 overview, sections 2.1, 3.2.1, 3.3.1 and 3.4. Defines the methodological distinctions used here; it does not validate the invented gardening probabilities.
Pearl · Causal inference in statisticsStark’s UC Berkeley course text distinguishes classification and observation from assigning a treatment.
Stark · Does treatment have an effect?NIST/SEMATECH section 5.3.3.1. Supports randomized design, not guaranteed realized baseline equality.
NIST · Completely randomized designsStark’s Stat 240 chapter 3. Motivates keeping fixed-card allocation uncertainty separate from fresh-population sampling.
Stark · Randomization modelsNIST/SEMATECH binomial distribution formulas. All chosen probabilities and numerical data belong to our synthetic rulebook.
NIST · Binomial distributionNIST’s Wilson formula. We do not use overlap of separate intervals as a treatment-difference test.
NIST · Confidence intervals for a proportionNIST explains coverage interpretation. Its mean-specific interval formula is not substituted for the binary Wilson calculation here.
NIST · Interpreting confidence limitsASA’s 2016 statement, six principles. A p-value is not the probability a hypothesis is true; this lesson’s model sampling probabilities are not p-values.
ASA · Statement on statistical significance and p-valuesIndependent subject review is pending.
Read the sources and model assumptionsRelease a few virtual balls, then a thousand. Change the chance of a right turn and compare the results with a mathematical prediction.
Interactive explorationTrain a real classifier on editable inspection cards. Reveal a confident mistake, repair a misleading shortcut, and freeze your model before opening its reserved test.
Interactive explorationOpen a genuinely trained miniature Transformer. Change token tiles, inspect real attention and vector calculations, sample a continuation, and test the limits of a confident prediction.