Empirical Methods for AI & CS Paul Cohen Ian P. Gent Toby Walsh [email protected]...

Empirical Methods for AI & CS

Paul Cohen Ian P. Gent Toby [email protected] [email protected] [email protected]

2

Overview

Introduction What are empirical methods? Why use them?

Case Study Eight Basic Lessons

Experiment design Data analysis How not to do it

Supplementary material

3

Resources

Web

www.cs.york.ac.uk/~tw/empirical.html

www.cs.amherst.edu/~dsj/methday.html Books

“Empirical Methods for AI”, Paul Cohen, MIT Press, 1995 Journals

Journal of Experimental Algorithmics, www.jea.acm.org Conferences

Workshop on Empirical Methods in AI (last Saturday, ECAI-02?)

Workshop on Algorithm Engineering and Experiments, ALENEX 01 (alongside SODA)

Empirical Methods for CS

Part I : Introduction

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What does “empirical” mean?

Relying on observations, data, experiments Empirical work should complement theoretical work

Theories often have holes (e.g., How big is the constant term? Is the current problem a “bad” one?)

Theories are suggested by observations Theories are tested by observations Conversely, theories direct our empirical attention

In addition (in this tutorial at least) empirical means “wanting to understand behavior of complex systems”

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Why We Need Empirical Methods Cohen, 1990 Survey of 150 AAAI Papers

Roughly 60% of the papers gave no evidence that the work they described had been tried on more than a single example problem.

Roughly 80% of the papers made no attempt to explain performance, to tell us why it was good or bad and under which conditions it might be better or worse.

Only 16% of the papers offered anything that might be interpreted as a question or a hypothesis.

Theory papers generally had no applications or empirical work to support them, empirical papers were demonstrations, not experiments, and had no underlying theoretical support.

The essential synergy between theory and empirical work was missing

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Theory, not Theorems

Theory based science need not be all theorems otherwise science would be mathematics

Consider theory of QED based on a model of behaviour of particles predictions accurate to many decimal places (9?)

most accurate theory in the whole of science? success derived from accuracy of predictions

not the depth or difficulty or beauty of theorems QED is an empirical theory!

8

Empirical CS/AI

Computer programs are formal objects so let’s reason about them entirely formally?

Two reasons why we can’t or won’t: theorems are hard some questions are empirical in nature

e.g. are Horn clauses adequate to represent the sort of knowledge met in practice?

e.g. even though our problem is intractable in general, are the instances met in practice easy to solve?

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Empirical CS/AI

Treat computer programs as natural objects like fundamental particles, chemicals, living organisms

Build (approximate) theories about them construct hypotheses

e.g. greedy hill-climbing is important to GSAT test with empirical experiments

e.g. compare GSAT with other types of hill-climbing refine hypotheses and modelling assumptions

e.g. greediness not important, but hill-climbing is!

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Empirical CS/AI

Many advantage over other sciences Cost

no need for expensive super-colliders Control

unlike the real world, we often have complete command of the experiment

Reproducibility in theory, computers are entirely deterministic

Ethics no ethics panels needed before you run experiments

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Types of hypothesis

My search program is better than yours

not very helpful beauty competition? Search cost grows exponentially with number of variables for

this kind of problem

better as we can extrapolate to data not yet seen? Constraint systems are better at handling over-constrained

systems, but OR systems are better at handling under-constrained systems

even better as we can extrapolate to new situations?

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A typical conference conversation

What are you up to these days?

I’m running an experiment to compare the Davis-Putnam algorithm with GSAT?

Why?

I want to know which is faster

Why?

Lots of people use each of these algorithms

How will these people use your result?...

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Keep in mind the BIG picture

What are you up to these days?

I’m running an experiment to compare the Davis-Putnam algorithm with GSAT?

Why?

I have this hypothesis that neither will dominate

What use is this?

A portfolio containing both algorithms will be more robust than either algorithm on its own

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Keep in mind the BIG picture

...

Why are you doing this?

Because many real problems are intractable in theory but need to be solved in practice.

How does your experiment help?

It helps us understand the difference between average and worst case results

So why is this interesting?

Intractability is one of the BIG open questions in CS!

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Why is empirical CS/AI in vogue?

Inadequacies of theoretical analysis problems often aren’t as hard in practice as theory predicts

in the worst-case average-case analysis is very hard (and often based on

questionable assumptions) Some “spectacular” successes

phase transition behaviour local search methods theory lagging behind algorithm design

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Why is empirical CS/AI in vogue?

Compute power ever increasing even “intractable” problems coming into range easy to perform large (and sometimes meaningful)

experiments Empirical CS/AI perceived to be “easier” than theoretical

CS/AI often a false perception as experiments easier to mess up

than proofs


Part II: A Case Study

Eight Basic Lessons

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Rosenberg study

“An Empirical Study of Dynamic Scheduling on Rings of Processors”

Gregory, Gao, Rosenberg & Cohen

Proc. of 8th IEEE Symp. on Parallel & Distributed Processing, 1996

Linked to from

www.cs.york.ac.uk/~tw/empirical.html

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Problem domain

Scheduling processors on ring network jobs spawned as binary trees

KOSO keep one, send one to my left

or right arbitrarily KOSO*

keep one, send one to my least heavily loaded neighbour

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Theory

On complete binary trees, KOSO is asymptotically optimal

So KOSO* can’t be any better?

But assumptions unrealistic tree not complete asymptotically not necessarily

the same as in practice!Thm: Using KOSO on a ring of p

processors, a binary tree of height n is executed within (2^n-1)/p + low order terms

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Benefits of an empirical study

More realistic trees probabilistic generator that makes shallow trees, which are

“bushy” near root but quickly get “scrawny” similar to trees generated when performing Trapezoid or

Simpson’s Rule calculationsbinary trees correspond to interval bisection

Startup costs network must be loaded

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Lesson 1: Evaluation begins with claimsLesson 2: Demonstration is good, understanding better

Hypothesis (or claim): KOSO takes longer than KOSO* because KOSO* balances loads better The “because phrase” indicates a hypothesis about why it

works. This is a better hypothesis than the beauty contest demonstration that KOSO* beats KOSO

Experiment design Independent variables: KOSO v KOSO*, no. of

processors, no. of jobs, probability(job will spawn), Dependent variable: time to complete jobs

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Criticism 1: This experiment design includes no direct measure of the hypothesized effect

Hypothesis: KOSO takes longer than KOSO* because KOSO* balances loads better

But experiment design includes no direct measure of load balancing: Independent variables: KOSO v KOSO*, no. of

processors, no. of jobs, probability(job will spawn), Dependent variable: time to complete jobs

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Lesson 3: Exploratory data analysis means looking beneath immediate results for explanations

T-test on time to complete jobs: t = (2825-2935)/587 = -.19 KOSO* apparently no faster than KOSO (as theory predicted) Why? Look more closely at the data:

Outliers create excessive variance, so test isn’t significant

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20

30

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50

60

70

80

10000 20000

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20

30

40

50

60

70

10000 20000

KOSO KOSO*

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Lesson 4: The task of empirical work is to explain variability

run-time

Algorithm (KOSO/KOSO*)

Number of processors

Number of jobs

“random noise” (e.g., outliers)

Number of processors and number of jobs explain 74% of the variance in run time. Algorithm explains almost none.

Empirical work assumes the variability in a dependent variable (e.g., run time) is the sum of causal factors and random noise. Statistical methods assign parts of this variability to the factors and the noise.

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Lesson 3 (again): Exploratory data analysis means looking beneath immediate results for explanations

Why does the KOSO/KOSO* choice account for so little of the variance in run time?

Unless processors starve, there will be no effect of load balancing. In most conditions in this experiment, processors never starved. (This is why we run pilot experiments!)

100 200 300

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20

30

100 200 300

10

20

30

40

50Queue length at processor i Queue length at processor i

KOSO KOSO*

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Lesson 5: Of sample variance, effect size, and sample size – control the first before touching the last

t x sN

magnitude of effect

backgroundvariance

sample size

This intimate relationship holds for all statistics

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Lesson 5 illustrated: A variance reduction method

Let N = num-jobs, P = num-processors, T = run timeThen T = k (N / P), or k multiples of the theoretical best timeAnd k = 1 / (N / P T)

k(KOSO) k(KOSO*)

102030405060708090

2 3 4 5

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20

30

40

50

60

70

2 3 4 5

t 1.61 1.4

.082.42, p .02

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Where are we?

KOSO* is significantly better than KOSO when the dependent variable is recoded as percentage of optimal run time

The difference between KOSO* and KOSO explains very little of the variance in either dependent variable

Exploratory data analysis tells us that processors aren’t starving so we shouldn’t be surprised

Prediction: The effect of algorithm on run time (or k) increases as the number of jobs increases or the number of processors increases

This prediction is about interactions between factors

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Lesson 6: Most interesting science is about interaction effects, not simple main effects

Data confirm prediction KOSO* is superior on larger

rings where starvation is an issue

Interaction of independent variables choice of algorithm number of processors

Interaction effects are essential to explaining how things work

1

2

3

3 6 10 20

number of processors

multiples of optimal run-time KOSO

KOSO*

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Lesson 7: Significant and meaningful are not synonymous. Is a result meaningful?

KOSO* is significantly better than KOSO, but can you use the result? Suppose you wanted to use the knowledge that the ring is controlled by

KOSO or KOSO* for some prediction. Grand median k = 1.11; Pr(trial i has k > 1.11) = .5 Pr(trial i under KOSO has k > 1.11) = 0.57 Pr(trial i under KOSO* has k > 1.11) = 0.43

Predict for trial i whether it’s k is above or below the median: If it’s a KOSO* trial you’ll say no with (.43 * 150) = 64.5 errors If it’s a KOSO trial you’ll say yes with ((1 - .57) * 160) = 68.8 errors If you don’t know you’ll make (.5 * 310) = 155 errors

155 - (64.5 + 68.8) = 22 Knowing the algorithm reduces error rate from .5 to .43. Is this enough???

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Lesson 8: Keep the big picture in mind

Why are you studying this?

Load balancing is important to get good performance out of parallel computers

Why is this important?

Parallel computing promises to tackle many of our computational bottlenecks

How do we know this? It’s in the first paragraph of the paper!

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Case study: conclusions

Evaluation begins with claims Demonstrations of simple main effects are

good, understanding the effects is better Exploratory data analysis means using your

eyes to find explanatory patterns in data The task of empirical work is to explain

variablitity Control variability before increasing sample

size Interaction effects are essential to explanations Significant ≠ meaningful Keep the big picture in mind


Part III : Experiment design

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Experimental Life Cycle

Exploration Hypothesis construction Experiment Data analysis Drawing of conclusions

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Checklist for experiment design*

Consider the experimental procedure making it explicit helps to identify spurious effects and sampling biases

Consider a sample data table identifies what results need to be collected clarifies dependent and independent variables shows whether data pertain to hypothesis

Consider an example of the data analysis helps you to avoid collecting too little or too much data especially important when looking for interactions

*From Chapter 3, “Empirical Methods for Artificial Intelligence”, Paul Cohen, MIT Press

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Guidelines for experiment design

Consider possible results and their interpretation may show that experiment cannot support/refute

hypotheses under test unforeseen outcomes may suggest new hypotheses

What was the question again? easy to get carried away designing an experiment and

lose the BIG picture Run a pilot experiment to calibrate parameters (e.g., number

of processors in Rosenberg experiment)

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Types of experiment

Manipulation experiment Observation experiment Factorial experiment

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Manipulation experiment

Independent variable, x x=identity of parser, size of dictionary, …

Dependent variable, y y=accuracy, speed, …

Hypothesis x influences y

Manipulation experiment change x, record y

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Observation experiment

Predictor, x x=volatility of stock prices, …

Response variable, y y=fund performance, …

Hypothesis x influences y

Observation experiment classify according to x, compute y

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Factorial experiment

Several independent variables, xi

there may be no simple causal links data may come that way

e.g. individuals will have different sexes, ages, ... Factorial experiment

every possible combination of xi considered expensive as its name suggests!

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Designing factorial experiments

In general, stick to 2 to 3 independent variables Solve same set of problems in each case

reduces variance due to differences between problem sets If this not possible, use same sample sizes

simplifies statistical analysis As usual, default hypothesis is that no influence exists

much easier to fail to demonstrate influence than to demonstrate an influence

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Some problem issues

Control Ceiling and Floor effects Sampling Biases

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Control

A control is an experiment in which the hypothesised variation does not occur so the hypothesized effect should not occur either

BUT remember placebos cure a large percentage of patients!

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Control: a cautionary tale

Macaque monkeys given vaccine based on human T-cells infected with SIV (relative of HIV) macaques gained immunity from SIV

Later, macaques given uninfected human T-cells and macaques still gained immunity!

Control experiment not originally done and not always obvious (you can’t control for all variables)

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Control: MYCIN case study

MYCIN was a medial expert system recommended therapy for blood/meningitis infections

How to evaluate its recommendations? Shortliffe used

10 sample problems, 8 therapy recommenders5 faculty, 1 resident, 1 postdoc, 1 student

8 impartial judges gave 1 point per problem max score was 80 Mycin 65, faculty 40-60, postdoc 60, resident 45, student 30

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Control: MYCIN case study

What were controls? Control for judge’s bias for/against computers

judges did not know who recommended each therapy Control for easy problems

medical student did badly, so problems not easy Control for our standard being low

e.g. random choice should do worse Control for factor of interest

e.g. hypothesis in MYCIN that “knowledge is power” have groups with different levels of knowledge

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Ceiling and Floor Effects

Well designed experiments (with good controls) can still go wrong

What if all our algorithms do particularly well Or they all do badly?

We’ve got little evidence to choose between them

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Ceiling and Floor Effects

Ceiling effects arise when test problems are insufficiently challenging floor effects the opposite, when problems too challenging

A problem in AI because we often repeatedly use the same benchmark sets most benchmarks will lose their challenge eventually? but how do we detect this effect?

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Machine learning example

14 datasets from UCI corpus of benchmarks used as mainstay of ML community

Problem is learning classification rules each item is vector of features and a classification measure classification accuracy of method (max 100%)

Compare C4 with 1R*, two competing algorithms

Rob Holte, Machine Learning, vol. 3, pp. 63-91, 1993

www.site.uottawa.edu/~holte/Publications/simple_rules.ps

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Floor effects: machine learning example

DataSet: BC CH GL G2 HD HE … Mean

C4 72 99.2 63.2 74.3 73.6 81.2 ... 85.9

1R* 72.5 69.2 56.4 77 78 85.1 ... 83.8

Is 1R* above the floor of performance?How would we tell?

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Floor effects: machine learning example

DataSet: BC CH GL G2 HD HE … Mean

C4 72 99.2 63.2 74.3 73.6 81.2 ... 85.9

1R* 72.5 69.2 56.4 77 78 85.1 ... 83.8

Baseline 70.3 52.2 35.5 53.4 54.5 79.4 … 59.9

“Baseline rule” puts all items in more popular category. 1R* is above baseline on most datasets

A bit like the prime number joke? 1 is prime. 3 is prime. 5 is prime. So, baseline rule isthat all odd numbers are prime.

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Ceiling Effects: machine learning

DataSet: BC GL HY LY MU … Mean

C4 72 63.2 99.1 77.5 100.0 ... 85.9

1R* 72.5 56.4 97.2 70.7 98.4 ... 83.8

How do we know that C4 and 1R* are not near the ceiling of

performance? Do the datasets have enough attributes to make perfect

classification? Obviously for MU, but what about the rest?

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DataSet: BC GL HY LY MU … Mean

C4 72 63.2 99.1 77.5 100.0 ... 85.9

1R* 72.5 56.4 97.2 70.7 98.4 ... 83.8

max(C4,1R*) 72.5 63.2 99.1 77.5 100.0 … 87.4

max([Buntine]) 72.8 60.4 99.1 66.0 98.6 … 82.0

C4 achieves only about 2% better than 1R*

Best of the C4/1R* achieves 87.4% accuracy We have only weak evidence that C4 better Both methods performing appear to be near ceiling of possible

so comparison hard!

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In fact 1R* only uses one feature (the best one) C4 uses on average 6.6 features 5.6 features buy only about 2% improvement Conclusion?

Either real world learning problems are easy (use 1R*) Or we need more challenging datasets We need to be aware of ceiling effects in results

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Sampling bias

Data collection is biased against certain data e.g. teacher who says “Girls don’t

answer maths question” observation might suggest:

girls don’t answer many questions

but that the teacher doesn’t ask them many questions

Experienced AI researchers don’t do that, right?

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Sampling bias: Phoenix case study

AI system to fight (simulated) forest fires

Experiments suggest that wind speed uncorrelated with time to put out fire obviously incorrect as high

winds spread forest fires

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Wind Speed vs containment time (max 150 hours):

3: 120 55 79 10 140 26 15 110 12 54 10 103

6: 78 61 58 81 71 57 21 32 70

9: 62 48 21 55 101 What’s the problem?

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The cut-off of 150 hours introduces sampling bias many high-wind fires get cut off, not many low wind

On remaining data, there is no correlation between wind speed and time (r = -0.53)

In fact, data shows that: a lot of high wind fires take > 150 hours to contain those that don’t are similar to low wind fires

You wouldn’t do this, right? you might if you had automated data analysis.

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Sampling biases can be subtle...

Assume gender (G) is an independent variable and number of siblings (S) is a noise variable.

If S is truly a noise variable then under random sampling, no dependency should exist between G and S in samples.

Parents have children until they get at least one boy. They don't feel the same way about girls. In a sample of 1000 girls the number with S = 0 is smaller than in a sample of 1000 boys.

The frequency distribution of S is different for different genders. S and G are not independent.

Girls do better at math than boys in random samples at all levels of education. Is this because of their genes or because they have more siblings? What else might be systematically associated with G that we don't know about?


Part IV: Data analysis

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Kinds of data analysis

Exploratory (EDA) – looking for patterns in data Statistical inferences from sample data

Testing hypotheses Estimating parameters

Building mathematical models of datasets Machine learning, data mining…

We will introduce hypothesis testing and computer-intensive methods

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The logic of hypothesis testing

Example: toss a coin ten times, observe eight heads. Is the coin fair (i.e., what is it’s long run behavior?) and what is your residual uncertainty?

You say, “If the coin were fair, then eight or more heads is pretty unlikely, so I think the coin isn’t fair.”

Like proof by contradiction: Assert the opposite (the coin is fair) show that the sample result (≥ 8 heads) has low probability p, reject the assertion, with residual uncertainty related to p.

Estimate p with a sampling distribution.

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Probability of a sample result under a null hypothesis

If the coin were fair (p= .5, the null hypothesis) what is the probability distribution of r, the number of heads, obtained in N tosses of a fair coin? Get it analytically or estimate it by simulation (on a computer): Loop K times

r := 0 ;; r is num.heads in N tosses

Loop N times ;; simulate the tosses• Generate a random 0 ≤ x ≤ 1.0• If x < p increment r ;; p is the probability of a head

Push r onto sampling_distribution Print sampling_distribution

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Sampling distributions

This is the estimated sampling distribution of r under the null hypothesis that p = .5. The estimation is constructed by Monte Carlo sampling.

10203040506070

0 1 2 3 4 5 6 7 8 9 10

Number of heads in 10 tosses

Frequency (K = 1000) Probability of r = 8 or moreheads in N = 10 tosses of afair coin is 54 / 1000 = .054

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The logic of hypothesis testing

Establish a null hypothesis: H0: p = .5, the coin is fair Establish a statistic: r, the number of heads in N tosses Figure out the sampling distribution of r given H0

The sampling distribution will tell you the probability p of a result at least as extreme as your sample result, r = 8

If this probability is very low, reject H0 the null hypothesis Residual uncertainty is p

0 1 2 3 4 5 6 7 8 9 10

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The only tricky part is getting the sampling distribution

Sampling distributions can be derived... Exactly, e.g., binomial probabilities for coins are given by

the formula

Analytically, e.g., the central limit theorem tells us that the sampling distribution of the mean approaches a Normal distribution as samples grow to infinity

Estimated by Monte Carlo simulation of the null hypothesis process

N!

r!(N r)!pN

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A common statistical test: The Z test for different means

A sample N = 25 computer science students has mean IQ m=135. Are they “smarter than average”?

Population mean is 100 with standard deviation 15 The null hypothesis, H0, is that the CS students are “average”,

i.e., the mean IQ of the population of CS students is 100. What is the probability p of drawing the sample if H0 were true?

If p small, then H0 probably false. Find the sampling distribution of the mean of a sample of size

25, from population with mean 100

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Central Limit Theorem:

The sampling distribution of the mean is given bythe Central Limit Theorem

The sampling distribution of the mean of samples of size N approaches a normal (Gaussian) distribution as N approaches infinity.

If the samples are drawn from a population with mean and standard deviation , then the mean of the sampling distribution is and its standard deviation is as N increases.

These statements hold irrespective of the shape of the original distribution.

x N

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The sampling distribution for the CS student example

If sample of N = 25 students were drawn from a population with mean 100 and standard deviation 15 (the null hypothesis) then the sampling distribution of the mean would asymptotically be normal with mean 100 and standard deviation 15 25 3

100 135

The mean of the CS students falls nearly 12 standard deviations away from the mean of the sampling distribution

Only ~1% of a normal distribution falls more than two standard deviations away from the mean

The probability that the students are “average” is roughly zero

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The Z test

100 135

Mean of sampling distribution

Samplestatistic

std=3

0 11.67


Teststatistic

std=1.0

Z x N

135 100

1525

353

11.67

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Reject the null hypothesis?

Commonly we reject the H0 when the probability of obtaining a sample statistic (e.g., mean = 135) given the null hypothesis is low, say < .05.

A test statistic value, e.g. Z = 11.67, recodes the sample statistic (mean = 135) to make it easy to find the probability of sample statistic given H0.

We find the probabilities by looking them up in tables, or statistics packages provide them.

For example, Pr(Z ≥ 1.67) = .05; Pr(Z ≥ 1.96) = .01.

Pr(Z ≥ 11) is approximately zero, reject H0.

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The t test

Same logic as the Z test, but appropriate when population standard deviation is unknown, samples are small, etc.

Sampling distribution is t, not normal, but approaches normal as samples size increases

Test statistic has very similar form but probabilities of the test statistic are obtained by consulting tables of the t distribution, not the normal

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The t test

100 135


Samplestatistic

std=12.1

0 2.89


Teststatistic

std=1.0

t x

sN

135 100

275

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12.12.89

Suppose N = 5 students have mean IQ = 135, std = 27

Estimate the standard deviation of sampling distribution using the sample standard deviation

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Summary of hypothesis testing

H0 negates what you want to demonstrate; find probability p of sample statistic under H0 by comparing test statistic to sampling distribution; if probability is low, reject H0 with residual uncertainty proportional to p.

Example: Want to demonstrate that CS graduate students are smarter than average. H0 is that they are average. t = 2.89, p ≤ .022

Have we proved CS students are smarter? NO! We have only shown that mean = 135 is unlikely if they aren’t. We

never prove what we want to demonstrate, we only reject H0, with residual uncertainty.

And failing to reject H0 does not prove H0, either!

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Common tests

Tests that means are equal Tests that samples are uncorrelated or independent Tests that slopes of lines are equal Tests that predictors in rules have predictive power Tests that frequency distributions (how often events happen) are

equal Tests that classification variables such as smoking history and

heart disease history are unrelated

... All follow the same basic logic

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Computer-intensive Methods

Basic idea: Construct sampling distributions by simulating on a computer the process of drawing samples.

Three main methods: Monte carlo simulation when one knows population parameters; Bootstrap when one doesn’t; Randomization, also assumes nothing about the population.

Enormous advantage: Works for any statistic and makes no strong parametric assumptions (e.g., normality)

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Another Monte Carlo example, relevant to machine learning...

Suppose you want to buy stocks in a mutual fund; for simplicity assume there are just N = 50 funds to choose from and you’ll base your decision on the proportion of J=30 stocks in each fund that increased in value

Suppose Pr(a stock increasing in price) = .75 You are tempted by the best of the funds, F, which reports

price increases in 28 of its 30 stocks. What is the probability of this performance?

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Simulate...

Loop K = 1000 times

B = 0 ;; number of stocks that increase in

;; the best of N funds

Loop N = 50 times ;; N is number of funds

H = 0 ;; stocks that increase in this fund

Loop M = 30 times ;; M is number of stocks in this fund

Toss a coin with bias p to decide whether this

stock increases in value and if so increment H

Push H on a list ;; We get N values of H

B := maximum(H) ;; The number of increasing stocks in

;; the best fund

Push B on a list ;; We get K values of B

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Surprise!

The probability that the best of 50 funds reports 28 of 30 stocks increase in price is roughly 0.4

Why? The probability that an arbitrary fund would report this increase is Pr(28 successes | pr(success)=.75)≈.01, but the probability that the best of 50 funds would report this is much higher.

Machine learning algorithms use critical values based on arbitrary elements, when they are actually testing the best element; they think elements are more unusual than they really are. This is why ML algorithms overfit.

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The Bootstrap

Monte Carlo estimation of sampling distributions assume you know the parameters of the population from which samples are drawn.

What if you don’t? Use the sample as an estimate of the population. Draw samples from the sample! With or without replacement? Example: Sampling distribution of the mean; check the

results against the central limit theorem.

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Bootstrapping the sampling distribution of the mean*

S is a sample of size N:

Loop K = 1000 times

Draw a pseudosample S* of size N from S by sampling with replacement

Calculate the mean of S* and push it on a list L L is the bootstrapped sampling distribution of the mean** This procedure works for any statistic, not just the mean.

* Recall we can get the sampling distribution of the mean via the central limit theorem – this example is just for illustration.

** This distribution is not a null hypothesis distribution and so is not directly used for hypothesis testing, but can easily be transformed into a null hypothesis distribution (see Cohen, 1995).

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Randomization

Used to test hypotheses that involve association between elements of two or more groups; very general.

Example: Paul tosses H H H H, Carole tosses T T T T is outcome independent of tosser?

Example: 4 women score 54 66 64 61, six men score 23 28 27 31 51 32. Is score independent of gender?

Basic procedure: Calculate a statistic f for your sample; randomize one factor relative to the other and calculate your pseudostatistic f*. Compare f to the sampling distribution for f*.

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Example of randomization

Four women score 54 66 64 61, six men score 23 28 27 31 51 32. Is score independent of gender?

f = difference of means of men’s and women’s scores: 29.25 Under the null hypothesis of no association between gender and score, the

score 54 might equally well have been achieved by a male or a female. Toss all scores in a hopper, draw out four at random and without replacement,

call them female*, call the rest male*, and calculate f*, the difference of means of female* and male*. Repeat to get a distribution of f*. This is an estimate of the sampling distribution of f under H0: no difference between male and female scores.


Part V: How Not To Do It

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Tales from the coal face

Those ignorant of history are doomed to repeat it we have committed many howlers

We hope to help others avoid similar ones …

… and illustrate how easy it is to screw up! “How Not to Do It”

I Gent, S A Grant, E. MacIntyre, P Prosser, P Shaw,

B M Smith, and T Walsh

University of Leeds Research Report, May 1997 Every howler we report committed by at least one of the

above authors!

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How Not to Do It

Do measure with many instruments in exploring hard problems, we used our best algorithms missed very poor performance of less good algorithms

better algorithms will be bitten by same effect on larger instances than we considered

Do measure CPU time in exploratory code, CPU time often misleading but can also be very informative

e.g. heuristic needed more search but was faster

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How Not to Do It

Do vary all relevant factors Don’t change two things at once

ascribed effects of heuristic to the algorithmchanged heuristic and algorithm at the same timedidn’t perform factorial experiment

but it’s not always easy/possible to do the “right” experiments if there are many factors

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How Not to Do It

Do Collect All Data Possible …. (within reason) one year Santa Claus had to repeat all our experiments

ECAI/AAAI/IJCAI deadlines just after new year! we had collected number of branches in search tree

performance scaled with backtracks, not branchesall experiments had to be rerun

Don’t Kill Your Machines we have got into trouble with sysadmins

… over experimental data we never used often the vital experiment is small and quick

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How Not to Do It

Do It All Again … (or at least be able to) e.g. storing random seeds used in experiments we didn’t do that and might have lost important result

Do Be Paranoid “identical” implementations in C, Scheme gave different

results Do Use The Same Problems

reproducibility is a key to science (c.f. cold fusion) can reduce variance

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Choosing your test data

We’ve seen the possible problem of over-fitting remember machine learning benchmarks?

Two common approaches benchmark libraries random problems

Both have potential pitfalls

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Benchmark libraries

+ve can be based on real problems lots of structure

-ve library of fixed size

possible to over-fit algorithms to library problems have fixed size

so can’t measure scaling

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Random problems

+ve problems can have any size

so can measure scaling can generate any number of problems

hard to over-fit? -ve

may not be representative of real problemslack structure

easy to generate “flawed” problemsCSP, QSAT, …

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Flawed random problems

Constraint satisfaction example 40+ papers over 5 years by many authors used Models A,

B, C, and D all four models are “flawed” [Achlioptas et al. 1997]

asymptotically almost all problems are trivialbrings into doubt many experimental results

• some experiments at typical sizes affected• fortunately not many

How should we generate problems in future?

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Flawed random problems

[Gent et al. 1998] fix flaw …. introduce “flawless” problem generation defined in two equivalent ways though no proof that problems are truly flawless

Undergraduate student at Strathclyde found new bug two definitions of flawless not equivalent

Eventually settled on final definition of flawless gave proof of asymptotic non-triviality so we think that we just about understand the problem

generator now

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Prototyping your algorithm

Often need to implement an algorithm usually novel algorithm, or variant of existing one

e.g. new heuristic in existing search algorithm novelty of algorithm should imply extra care more often, encourages lax implementation

it’s only a preliminary version

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How Not to Do It

Don’t Trust Yourself bug in innermost loop found by chance all experiments re-run with urgent deadline curiously, sometimes bugged version was better!

Do Preserve Your Code Or end up fixing the same error twice

Do use version control!

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How Not to Do It

Do Make it Fast Enough emphasis on enough

it’s often not necessary to have optimal codein lifecycle of experiment, extra coding time not won back

e.g. we have published many papers with inefficient codecompared to state of the art

• first GSAT version O(N2), but this really was too slow!• Do Report Important Implementation Details

Intermediate versions produced good results

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How Not to Do It

Do Look at the Raw Data Summaries obscure important aspects of behaviour Many statistical measures explicitly designed to minimise

effect of outliers Sometimes outliers are vital

“exceptionally hard problems” dominate meanwe missed them until they hit us on the head

when experiments “crashed” overnight

old data on smaller problems showed clear behaviour

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How Not to Do It

Do face up to the consequences of your results e.g. preprocessing on 450 problems

should “obviously” reduce searchreduced search 448 timesincreased search 2 times

Forget algorithm, it’s useless? Or study in detail the two exceptional cases

and achieve new understanding of an important algorithm


Part VII : Coda

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Our objectives

Outline some of the basic issues exploration, experimental design, data analysis, ...

Encourage you to consider some of the pitfalls we have fallen into all of them!

Raise standards encouraging debate identifying “best practice”

Learn from your experiences experimenters get better as they get older!

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Summary

Empirical CS and AI are exacting sciences There are many ways to do experiments wrong

We are experts in doing experiments badly As you perform experiments, you’ll make many mistakes Learn from those mistakes, and ours!


Part VII : Supplement

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Some expert advice

Bernard Moret, U. New Mexico

“Towards a Discipline of Experimental Algorithmics” David Johnson, AT&T Labs

“A Theoretician’s Guide to the Experimental Analysis of Algorithms”

Both linked to from www.cs.york.ac.uk/~tw/empirical.html

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Bernard Moret’s guidelines

Useful types of empirical results: accuracy/correctness of

theoretical results real-world performance heuristic quality impact of data structures ...

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Hallmarks of a good experimental paper clearly defined goals large scale tests

both in number and size of instances mixture of problems

real-world, random, standard benchmarks, ... statistical analysis of results reproducibility

publicly available instances, code, data files, ...

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Pitfalls for experimental papers simpler experiment would have given same result result predictable by (back of the envelope) calculation bad experimental setup

e.g. insufficient sample size, no consideration of scaling, …

poor presentation of data

e.g. lack of statistics, discarding of outliers, ...

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Ideal experimental procedure define clear set of objectives

which questions are you asking? design experiments to meet these objectives collect data

do not change experiments until all data is collected to prevent drift/bias

analyse data

consider new experiments in light of these results

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David Johnson’s guidelines

3 types of paper describe the implementation of an algorithm application paper

“Here’s a good algorithm for this problem”

sales-pitch paper

“Here’s an interesting new algorithm”

experimental paper

“Here’s how this algorithm behaves in practice”

These lessons apply to all 3

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Perform “newsworthy” experiments standards higher than for theoretical papers! run experiments on real problems

theoreticians can get away with idealized distributions but experimentalists have no excuse!

don’t use algorithms that theory can already dismiss look for generality and relevance

don’t just report algorithm A dominates algorithm B, identify why it does!

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Place work in context compare against previous work in literature ideally, obtain their code and test sets

verify their results, and compare with your new algorithm less ideally, re-implement their code

report any differences in performance least ideally, simply report their old results

try to make some ball-park comparisons of machine speeds

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Use efficient implementations “somewhat” controversial efficient implementation supports claims of practicality

tells us what is achievable in practice can run more experiments on larger instances

can do our research quicker! don’t have to go over-board on this exceptions can also be made

e.g. not studying CPU time, comparing against a previously newsworthy algorithm, programming time more valuable than processing time, ...

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Use testbeds that support general conclusions ideally one (or more) random class, & real world instances

predict performance on real world problems based on random class, evaluate quality of predictions

structured random generators

parameters to control structure as well as size don’t just study real world instances

hard to justify generality unless you have a very broad class of real world problems!

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Provide explanations and back them up with experiment adds to credibility of experimental results improves our understanding of algorithms

leading to better theory and algorithms can “weed” out bugs in your implementation!

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Ensure reproducibilty easily achieved via the Web adds support to a paper if others can (and do) reproduce

the results requires you to use large samples and wide range of

problems

otherwise results will not be reproducible!

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Ensure comparability (and give the full picture) make it easy for those who come after to reproduce your

results provide meaningful summaries

give sample sizes, report standard deviations, plot graphs but report data in tables in the appendix

do not hide anomalous results report running times even if this is not the main focus

readers may want to know before studying your results in detail

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David Johnson’s pitfalls

Failing to report key implementation details Extrapolating from tiny samples Using irreproducible benchmarks Using running time as a stopping criterion Ignoring hidden costs (e.g. preprocessing) Misusing statistical tools Failing to use graphs

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David Johnson’s pitfalls

Obscuring raw data by using hard-to-read charts Comparing apples and oranges Drawing conclusions not supported by the data Leaving obvious anomalies unnoted/unexplained Failing to back up explanations with further experiments Ignoring the literature

the self-referential study!

Empirical Methods for AI & CS Paul Cohen Ian P. Gent Toby Walsh [email protected]...

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Transcript of Empirical Methods for AI & CS Paul Cohen Ian P. Gent Toby Walsh [email protected]...