Pattern recognition. Practices, perspectives and challenges

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It is on this background that I would like to highlight two aspects of validation and crossvalidation that do not seem to be fully appreciated in the larger community of applied machine learning practitioners: i the need for correct and strict procedure in validation or crossvalidation and ii the need for careful interpretation of validation results if multiple studies use the same reference data set.

Both issues are different aspects of the same problem of overfitting and hence closely related, but while the former has known solutions that applied researchers can be informed about the latter is more involved and invites further research by machine learning experts. The idea of validation in pattern recognition rests on the principle that separate data are used to develop a method the training set and to subsequently test its performance the test set. This principle has been established to avoid overfitting, i. To avoid overfitting and give a reasonable prediction of the performance of a method on new unseen data, the correct procedure stipulates that the test data shall not be used in any way for training the classifier or developing the classification method.

The same principle applies to crossvalidation in which training and test sets are formed repeatedly by splitting a single available data set see Figure 1 for an introduction. This principle of strict validation is well known; yet, in the last year alone, I have encountered three violations of the principle in published and unpublished work. Figure 1. Diagrammatic illustration of validation A and crossvalidation B—D methods. A Normal validation with a true test set holdout set. A part of the data purple is permanently withheld from training and used for testing after training has been completed.

B k -fold crossvalidation. The data are divided into k parts folds and one of the folds is withheld from training and used for testing purple. The procedure is repeated until all folds have been withheld once and the average error is reported. C Stratified crossvalidation.

In stratified crossvalidation, the folds are formed so that they contain the same proportion of members of each class as much as this is possible , indicated by the purple slices taken from each class. Crossvalidation then proceeds as described in B. The variability of error estimates that arises from the choice of folds is reduced in stratified crossvalidation.

D Inner and outer crossvalidation for feature selection. If feature selection is itself based on crossvalidation, e. In this example, researchers investigated a new method for recognizing odors with an electronic nose, eventually employing a support vector machine SVM algorithm with radial basis function RBF kernel on the data collected with their novel method.

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To adjust the meta-parameters of the SVM, they ran a grid search of parameters using crossvalidation with their entire data set to judge parameter suitability. The study then proceeded to use the identified meta-parameters to report crossvalidation results for classification performance.

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In this example, the research was focused on characterizing how well the spiking activity of an identified neuron in the brain of crickets would represent the quality of a stimulus. The researchers used activity from within a time window and crossvalidation of a naive Bayes classifier to determine how well the neuronal activity could predict whether a stimulus was attractive or not.

This was repeated for different time window sizes and the performance of the classifier for the best time window was reported. Doing so inadvertently created the impression that the animal may be able to perform at the reported best performance level when utilizing the activity of the neuron in question. However, such a conclusion is not supported by the study because the same data were used for model selection selecting the observation time window and final crossvalidation. In this example, published work on pattern recognition of high-dimensional data from gas chromatography and mass spectrometry for the analysis of human breath involved a preprocessing pipeline including a statistical test for selecting significant features, principal component analysis PCA , and canonical analysis CA.

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Data preprocessing was performed on the entire data set and subsequently the performance of a kNN classifier was evaluated in crossvalidation. This is a clear violation of the principle of strict separation of training and test sets. In this example, we were able to get an estimate for the possible impact of overfitting by using our own data of similar nature Berna et al. We collected the breath of 10 healthy adults on 4 days each, with 3 repetitions each day, and analyzed it with a commercial enose. If we used LOO crossvalidation more strictly for the entire procedure of feature selection and classification, the error rate increased to Much worse, when we performed crossvalidation so that strictly all 3 repetitions from a day were removed together stratified fold crossvalidation , the error rate was worse than chance levels These numbers illustrate that the correct procedure for crossvalidation in the context of high-dimensional data, few samples, and long processing pipelines is not just a detail but can determine success or failure of a method.

It is essential that this knowledge is passed on to applied researchers with the increasing popularity of machine learning methods in applications [see also Ransohoff , Broadhurst and Kell , and Marco ].

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Furthermore, it is important to be clear that any use of the test or holdout data introduces serious risks of overfitting. Adjusting meta-parameters. If crossvalidation is used for adjusting meta-parameters, an inner and outer crossvalidation procedure must be performed see Figure 1 D. Model selection. Testing different methods with crossvalidation and reporting the best one constitutes overfitting because the holdout sets are used in choosing the method. Excluding outliers.

If the identification of outliers depends on their relationship to other inputs, test data should not be included in the decision process. Clustering or dimensionality reduction. These preprocessing methods should only have access to training data. Statistical tests.

Pattern Recognition: Practices, Perspectives and Challenges-西安交通大学图书馆

If using statistical tests for feature selection, test data cannot be included. We have seen above that problems with the correct use of validation methods occur, in particular in applied work, which can be addressed by adhering to established correct procedures. However, I would like to argue that beyond the established best practice, there is also room for further research on the risks of overfitting in the area of collaborative work on representative data sets.

When doing so it would be natural to expect a performance close to the reported validation accuracy from the table. Therefore, if we use the reported studies for model selection we inadvertently introduce a risk of overfitting. The practical implication is that we cannot be sure to have truly selected the best method and we do not know whether and how much the reported accuracy estimate may be inflated by overfitting. When Fung et al. They found that the best predicted accuracy for the repeated crossvalidation with different algorithms varied from 0. The crossvalidation estimates of accuracy in this example are hence largely over-optimistic, and this is already the case for only 10 tested algorithms the MNIST table reports 69 different algorithms.

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Related work by Isaksson et al. Assuming no prior knowledge, the posterior distribution underlying Bayesian confidence intervals only depends on the number of correct predictions and the total number of test samples, so that we can calculate confidence intervals for the MNIST results directly from the published table LeCun and Cortes, Figure 2 A shows the results. As indicated by the gray bar, all methods to the right of the vertical dashed line have confidence intervals that overlap with the confidence interval of the best method.

We can interpret this as an indication that they should probably be treated as equivalent. Figure 2. The confidence intervals were calculated assuming no prior knowledge on the classification accuracy, and for confidence level 0. The gray bar indicates the confidence interval for the best method and the dashed line separates the methods whose confidence intervals intersect with the bar from the rest. Bullets are the mean observed fraction and errorbars the standard deviation across all values of k most errorbars are too small to be visible.

For values of n sub of and above, this fraction is 0 for all k , i. C—W Illustration of the synthetic data experiment with random vectors underlying B. C—F example training C,D and test E,F sets for random vectors of class 0 red and 1 blue for unstructured training and test sets. C,E are the worst performing example out of 50 repetitions and D,F the example where the classifiers perform best. G Histogram of the observed distribution of occurrence of the optimal k value in kNN classification of the test set. H Histogram of the distribution of observed classification accuracies for the test set, pooled for all k.

J—P Same plots as C—I for training and test sets that consist of 50 sub-classes. Q—W Same plots for training and test sets that consist of 2 sub-classes. Attaching confidence intervals to the predicted accuracies is an important step forward both for underpinning the selection process and the judgment on the expected accuracy of the selected method.

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However, it is important to be aware that the proposed Bayesian confidence intervals rest on the assumption that the test samples are all statistically independent. The MNIST digits were written by separate writers who will have different ways of writing each of the digits and variations between writers would be larger than variations between repeated symbols from the same writer. To investigate whether such correlations could have an effect on the validity of confidence intervals, I have created the following synthetic problem. Figures 2 C,D show two examples of training sets and 2E,F of test sets.

I test each classifier on the independent test set, from which we can determine the expected performance as it would be reported in the MNIST table. Because the data are purely synthetic, I can generate as many of these experiments as I would like, which would correspond to an arbitrary number of MNIST sets in the analogy. When I repeat the described experiment with independently generated training and test sets, I observe the effects illustrated in Figures 2 G—I.

The k value leading to the best performance varies between instances Figure 2 G , and so does the distribution of achieved maximal performance Figure 2 H. Furthermore, the posterior distribution underlying the Bayesian confidence interval corresponds well with the observed distribution of performances Figure 2 I. In summary, for the synthetic data with fully independent samples, the Bayesian confidence intervals with naive prior work very well, as expected.

Each such sub-cloud would correspond to the digits written by a different person in the MNIST analogy.

Conventional methods and future directions

The standard deviation in the unstructured example above was chosen to match the overall standard deviation of the structured samples here. The differences to the unstructured case are quite drastic Figures 2 J—W. The preference for large k in successful classifiers diminishes until there is no preferred value for 2 sub-classes. It rises from zero for the unstructured case to its maximal value of This indicates that Gaussian confidence intervals of this kind are surprisingly vulnerable to correlations in the data. I should repeat at this point that this discussion is not about criticizing the work with the MNIST data set, which has been very valuable to the field, and I have used MNIST myself in the context of bio-mimetic classification Huerta and Nowotny, ; Nowotny et al.

The problem that I am trying to expose is that while some headway has been made with investigating the possible bias in model selection Fung et al. One radical solution to the problem would be to ban testing on the same test set altogether. However, this leads to a difficult contradiction: to make fair comparisons, we need to compare algorithms on equal terms the same training and test set but due to the discussed unknown biases, we would rather like to avoid using the same training and test set multiple times.