cross-validationscikit learn
As per scikit-learn's example on the interpretability of the learning curve, the following figure suggests that the SVM model requires more training examples to improve the validation score.
My question is, how is the need for more training examples justified when both the training score and the validation score are near perfect?
From section 7.10.2 of Elements of Statistical Learning(free online, and it's great):
Consider a classification problem with a large number of predictors, as may arise, for example, in genomic or proteomic applications. A typical strategy for analysis might be as follows:
Is this a correct application of cross-validation? Consider a scenario with N = 50 samples in two equal-sized classes, and p = 5000 quantitative predictors (standard Gaussian) that are independent of the class labels. The true (test) error rate of any classifier is 50%. We carried out the above recipe, choosing in step (1) the 100 predictors having highest correlation with the class labels, and then using a 1-nearest neighbor classifier, based on just these 100 predictors, in step (2). Over 50 simulations from this setting, the average CV error rate was 3%. This is far lower than the true error rate of 50%.
What has happened? The problem is that the predictors have an unfair advantage, as they were chosen in step (1) on the basis of all of the samples. Leaving samples out after the variables have been selected does not cor-rectly mimic the application of the classifier to a completely independent test set, since these predictors “have already seen” the left out samples.
We selected the 100 predictors having largest correlation with the class labels over all 50 samples. Then we chose a random set of 10 samples, as we would do in five-fold cross-validation, and computed the correlations of the pre-selected 100 predictors with the class labels over just these 10 samples (top panel). We see that the correlations average about 0.28, rather than 0, as one might expect
I'm not sure what you want to do in step 7a. As I understand it right now, it doesn't make sense to me.
Here's how I understand your description: in step 7, you want to compare the hold-out performance with the results of a cross validation embracing steps 4 - 6. (so yes, that would be a nested setup).
The main points why I don't think this comparison makes much sense are:
This comparison cannot detect two of the main sources of overoptimistic validation results I encounter in practice:
data leaks (dependence) between training and test data which is caused by a hierarchical (aka clustered) data structure, and which is not accounted for in the splitting. In my field, we have typically multiple (sometimes thousands) of readings (= rows in the data matrix) of the same patient or biological replicate of an experiment. These are not independent, so the validation splitting needs to be done at patient level. However, such a data leak occurs, you'll have it both in the splitting for the hold out set and in the cross validation splitting. Hold-out wold then be just as optimistically biased as cross validation.
Preprocessing of the data done on the whole data matrix, where the calculations are not independent for each row but many/all rows are used to calculation parameters for the preprocessing. Typical examples would be e.g. a PCA projection before the "actual" classification.
Again, that would affect both your hold-out and the outer cross validation, so you cannot detect it.
For the data I work with, both errors can easily cause the fraction of misclassifications to be underestimated by an order of magnitude!
If you are restricted to this counted fraction of test cases type of performance, model comparisons need either extremely large numbers of test cases or ridiculously large differences in true performance. Comparing 2 classifiers with unlimited training data may be a good start for further reading.
However, comparing the model quality the inner cross validation claims for the "optimal" model and the outer cross validation or hold out validation does make sense: if the discrepancy is high, it is questionable whether your grid search optimization did work (you may have skimmed variance due to the high variance of the performance measure). This comparison is easier in that you can spot trouble if you have the inner estimate being ridiculously good compared to the other - if it isn't, you don't need to worry that much about your optimization. But in any case, if your outer (7) measurement of the performance is honest and sound, you at least have a useful estimate of the obtained model, whether it is optimal or not.
IMHO measuring the learning curve is yet a different problem. I'd probably deal with that separately, and I think you need to define more clearly what you need the learning curve for (do you need the learning curve for a data set of the given problem, data, and classification method or the learning curve for this data set of the given problem, data, and classification mehtod), and a bunch of further decisions (e.g. how to deal with the model complexity as function of the training sample size? Optimize all over again, use fixed hyperparameters, decide on function to fix hyperparameters depending on training set size?)
(My data usually has so few independent cases to get the measurement of the learning curve sufficiently precise to use it in practice - but you may be better of if your 1200 rows are actually independent)
First of all, nothing is wrong with nested cross validation here. Nested validation is of utmost importance for data-driven optimization, and cross validation is a very powerful approaches (particularly if iterated/repeated).
Then, whether anything is wrong at all depends on your point of view: as long as you do an honest nested validation (keeping the outer test data strictly independent), the outer validation is a proper measure of the "optimal" model's performance. Nothing wrong with that.
But several things can and do go wrong with grid search of these proportion-type performance measures for hyperparameter tuning of SVM. Basically they mean that you may (probably?) cannont rely on the optimization. Nevertheless, as long as your outer split was done properly, even if the model is not the best possible, you have an honest estimate of the performance of the model you got.
I'll try to give intuitive explanations why the optimization may be in trouble:
Mathematically/statisticaly speaking, the problem with the proportions is that measured proportions $\hat p$ are subject to a huge variance due to finite test sample size $n$ (depending also on the true performance of the model, $p$):
$Var (\hat p) = \frac{p (1 - p)}{n}$
You need ridiculously huge numbers of cases (at least compared to the numbers of cases I can usually have) in order to achieve the needed precision (bias/variance sense) for estimating recall, precision (machine learning performance sense). This of course applies also to ratios you calculate from such proportions. Have a look at the confidence intervals for binomial proportions. They are shockingly large! Often larger than the true improvement in performance over the hyperparameter grid. And statistically speaking, grid search is a massive multiple comparison problem: the more points of the grid you evaluate, the higher the risk of finding some combination of hyperparameters that accidentally looks very good for the train/test split you are evaluating. This is what I mean with skimming variance. The well known optimistic bias of the inner (optimization) validation is just a symptom of this variance skimming.
Intuitively, consider a hypothetical change of a hyperparameter, that slowly causes the model to deteriorate: one test case moves towards the decision boundary. The 'hard' proportion performance measures do not detect this until the case crosses the border and is on the wrong side. Then, however, they immediately assign a full error for an infinitely small change in the hyperparameter.
In order to do numerical optimization, you need the performance measure to be well behaved. That means: neither the jumpy (not continously differentiable) part of the proportion-type performance measure nor the fact that other than that jump, actually occuring changes are not detected are suitable for the optimization.
Proper scoring rules are defined in a way that is particularly suitable for optimization. They have their global maximum when the predicted probabilities match the true probabilities for each case to belong to the class in question.
For SVMs you have the additional problem that not only the performance measures but also the model reacts in this jumpy fashion: small changes of the hyperparameter will not change anything. The model changes only when the hyperparameters are changes enough to cause some case to either stop being support vector or to become support vector. Again, such models are hard to optimize.
Literature:
Brereton, R.: Chemometrics for pattern recognition, Wiley, (2009).
points out the jumpy behaviour of the SVM as function of the hyperparameters.
what you can afford in terms of model comparison obviously depends on the number of independent cases. Let's make some quick and dirty simulation about the risk of skimming variance here:
scikit.learn says that they have 1797 are in the digits data.
i.e., all models have the same true performance of, say, 97 % (typical performance for the digits data set).
Run $10^4$ simulations of "testing these models" with sample size = 1797 rows in the digits data set
p.true = 0.97 # hypothetical true performance for all models
n.models = 100 # 10 x 10 grid
n.rows = 1797 # rows in scikit digits data
sim.test <- replicate (expr= rbinom (n= nmodels, size= n.rows, prob= p.true),
n = 1e4)
sim.test <- colMaxs (sim.test) # take best model
hist (sim.test / n.rows,
breaks = (round (p.true * n.rows) : n.rows) / n.rows + 1 / 2 / n.rows,
col = "black", main = 'Distribution max. observed performance',
xlab = "max. observed performance", ylab = "n runs")
abline (v = p.outer, col = "red")
Here's the distribution for the best observed performance:
The red line marks the true performance of all our hypothetical models. On average, we observe only 2/3 of the true error rate for the seemingly best of the 100 compared models (for the simulation we know that they all perform equally with 97% correct predictions).
This simulation is obviously very much simplified:
In general, however, both low number of independent test cases and high number of compared models increase the bias. Also, the Cawley and Talbot paper gives empirical observed behaviour.
Best Answer
Why do they say more training cases are needed?
Training error being better than error on any kind of data that was independent of the training (test set, cross validation, out of bootstrap,...) is a symptom of overfitting, so the primary diagnosis here is overfitting.
One possibility to reduce overfitting is to get more training data.
Another possibility here would be to plot for, say, 1400 cases training and generalization error over γ to see at which γ the training error starts to move away from 0 (more restrictive model).
With near perfect cross validation results it is of course difficult to see whether training error starts to lower itself in direction of the CV error. Looking at the numbers may help here. I tend to consider both the absolute and difference between training and test performance and $\frac{test~error}{training~error}$ ratio: there may still be an order of magnitude between them here.
Do we really need more cases?
In practice, I'd recommend to check the estimated performance against application needs - if you need better than 98% accuracy, you're fine here. If you need to demonstrate $\geq$ 99.5% accuracy, you need more cases (probably many more, if you consider also the test sample size requirements for a one-sided confidence interval).