Transcript Empirical Methods for AI and CS - School of Computer Science and

Empirical Methods for AI & CS
Paul Cohen
Ian P. Gent
Toby Walsh
[email protected]
[email protected]
[email protected]
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
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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)
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Empirical Methods for CS
Part I :
Introduction
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!
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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 underconstrained 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
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Empirical Methods for CS
Part II:
A Case Study
Eight Basic Lessons
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 calculations
 binary trees correspond to interval bisection
 Startup costs
 network must be loaded
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Lesson 1: Evaluation begins with claims
Lesson 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:
80
70
70
60
60
50
40
50
KOSO
40
30
30
20
20
10
10
10000
20000
KOSO*
10000
20000
 Outliers create excessive variance, so test isn’t significant
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Lesson 4: The task of empirical work is to explain
variability
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.
Algorithm (KOSO/KOSO*)
Number of processors
run-time
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.
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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?
Queue length at processor i
50
KOSO
40
Queue length at processor i
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KOSO*
20
30
20
10
10
100
200
300
100
200
300
 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!)
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Lesson 5: Of sample variance, effect size, and sample
size – control the first before touching the last
magnitude of effect
x-m
t =
s
sample size
N
background
variance
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 time
Then T = k (N / P), or k multiples of the theoretical best time
And k = 1 / (N / P T)
1.61 - 1.4
t=
= 2.42, p  .02
.08
90
80
70
60
50
40
30
20
10
70
60
50
40
30
20
10
2
3
k(KOSO)
4
5
2
3
4
5
k(KOSO*)
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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
3
2
multiples of
optimal run-time
KOSO
KOSO*
 Data confirm prediction
 KOSO* is superior on larger
rings where starvation is an
issue
 Interaction of independent
variables
 choice of algorithm
 number of processors
1
3
6
10
20
number of processors
 Interaction effects are essential to
explaining how things work
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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
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Empirical Methods for CS
Part III :
Experiment design
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 recommenders
 5 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:
C4
1R*
BC
72
72.5
CH
99.2
69.2
GL
63.2
56.4
G2
74.3
77
HD
73.6
78
HE
81.2
85.1
…
...
...
Mean
85.9
83.8
Is 1R* above the floor of performance?
How would we tell?
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Floor effects: machine learning example
DataSet:
C4
1R*
Baseline
BC
72
72.5
70.3
CH
99.2
69.2
52.2
GL
63.2
56.4
35.5
G2
74.3
77
53.4
HD
73.6
78
54.5
HE
81.2
85.1
79.4
…
...
...
…
Mean
85.9
83.8
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 is
that all odd numbers are prime.
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Ceiling Effects: machine learning
DataSet:
C4
1R*
BC
72
72.5
GL
63.2
56.4
HY
99.1
97.2
LY
77.5
70.7
MU …
100.0 ...
98.4 ...
Mean
85.9
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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Ceiling Effects: machine learning
DataSet:
C4
1R*
max(C4,1R*)
max([Buntine])
BC
72
72.5
72.5
72.8
GL
63.2
56.4
63.2
60.4
HY
99.1
97.2
99.1
99.1
LY
77.5
70.7
77.5
66.0
MU
100.0
98.4
100.0
98.6
…
...
...
…
…
Mean
85.9
83.8
87.4
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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Ceiling Effects: machine learning




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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Sampling bias: Phoenix case study
 Wind Speed vs containment time (max 150 hours):
3: 120
55
79
10
140 26
15
110
54 10
103
6: 78
61
58
81
71
57
21
32
9: 62
48
21
55
101
 What’s the problem?
12
70
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Sampling bias: Phoenix case study
 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?
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Empirical Methods for CS
Part IV:
Data analysis
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
Frequency (K = 1000)
Probability of r = 8 or more
heads in N = 10 tosses of a
fair coin is 54 / 1000 = .054
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60
50
40
30
20
10
0
1
2
3
4
5 6
7
8
9 10
Number of heads in 10 tosses
This is the estimated sampling distribution of r under the
null hypothesis that p = .5. The estimation is constructed by
Monte Carlo sampling.
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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
0
1
2
3
4
5 6
7
8
9 10
 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
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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
N!
N
r!( N - r)!
p
 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
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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 by
the 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 m and
standard deviation , then the mean of the sampling distribution
is m and its standard deviation is  x =  N as N increases.
These statements hold irrespective of the shape of the original
distribution.
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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
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
100
135
The probability that the students are
“average” is roughly zero
70
The Z test
Mean of sampling
distribution
Sample
statistic
Mean of sampling
distribution
std=3
100
std=1.0
135
Z=
Test
statistic
x-m

N
=
0
11.67
135 - 100 35
= = 11.67
15
3
25
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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
73
The t test
Suppose N = 5 students have mean IQ = 135, std = 27
Estimate the standard
deviation of sampling
distribution using the sample
standard deviation
Mean of sampling
distribution
x - m 135 - 100 35
t=
=
=
= 2.89
s
27
12.1
N
5
Sample
statistic
Mean of sampling
distribution
std=12.1
100
135
Test
statistic
std=1.0
0
2.89
74
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
76
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)
77
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?
78
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.
80
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.
81
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
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can easily be transformed into a null hypothesis distribution (see Cohen, 1995).
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*.
83
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.
84
Empirical Methods for CS
Part V:
How Not To Do It
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!
86
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
87
How Not to Do It
 Do vary all relevant factors
 Don’t change two things at once
 ascribed effects of heuristic to the algorithm
 changed heuristic and algorithm at the same time
 didn’t perform factorial experiment
 but it’s not always easy/possible to do the “right”
experiments if there are many factors
88
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 branches
 all 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
89
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
90
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
91
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
92
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 problems
 lack structure
 easy to generate “flawed” problems
 CSP, QSAT, …
93
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 trivial
 brings into doubt many experimental results
• some experiments at typical sizes affected
• fortunately not many
 How should we generate problems in future?
94
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
95
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
96
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!
97
How Not to Do It
 Do Make it Fast Enough
 emphasis on enough
 it’s often not necessary to have optimal code
 in lifecycle of experiment, extra coding time not won back
 e.g. we have published many papers with inefficient code
 compared 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
98
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 mean
 we missed them until they hit us on the head
when experiments “crashed” overnight
old data on smaller problems showed clear behaviour
99
How Not to Do It
 Do face up to the consequences of your results
 e.g. preprocessing on 450 problems
 should “obviously” reduce search
 reduced search 448 times
 increased search 2 times
 Forget algorithm, it’s useless?
 Or study in detail the two exceptional cases
 and achieve new understanding of an important
algorithm
100
Empirical Methods for CS
Part VII :
Coda
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!
102
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!
103
Empirical Methods for CS
Part VII :
Supplement
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
105
Bernard Moret’s guidelines
 Useful types of empirical results:
 accuracy/correctness of
theoretical results
 real-world performance
 heuristic quality
 impact of data structures
 ...
106
Bernard Moret’s guidelines
 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, ...
107
Bernard Moret’s guidelines
 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, ...
108
Bernard Moret’s guidelines
 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
109
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
110
David Johnson’s guidelines
 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!
111
David Johnson’s guidelines
 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
112
David Johnson’s guidelines
 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, ...
113
David Johnson’s guidelines
 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!
114
David Johnson’s guidelines
 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!
115
David Johnson’s guidelines
 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!
116
David Johnson’s guidelines
 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
117
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
118
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!
119