An Odd Set of Odds in Kinship Matching with DNA Databases

The 22d International Symposium on the Future of Human Identification began yesterday with a set of workshops. One was on "familial searching." The phrase refers to trawling the profiles in a DNA database for certain types of partial matches to a DNA profile from a crime-scene sample.

Partial matches that are useful in generating investigative leads to family members arise much more often when a particular kind of relative (say, a full sibling) is the source of the crime-scene sample than when an individual who is not closely related to the database inhabitant is the source. The ratio of the probability of the partial match under the former condition (a given genetic relationship) to the latter (unrelated individuals) is a likelihood ratio (LR). The LR (or, technically, its logarithm) for siblingship expresses the weight of the evidence in favor of the hypothesis that the source is full sibling as opposed to an unrelated individual.

After explaining the this idea, the first speaker presented the following formula:

"Odds" = LR_autosomal x LR_Y-STR x 1/N         (1)

She attributed this formula to the California state DNA laboratory that does familial searching in that state. In this equation, N is the size of the database, LR_autosomal is the likelihood ratio for the partial match at a set of autosomal STR loci, and LR_Y-STR is the likelihood ratio for the matching Y-STR haplotype.

She described this as a Bayesian computation that could lead to statements in court such as "there is a 98% probability" that the person whose DNA was found at the crime scene is a brother of Joe Smith, a convicted offender whose DNA profile is in a DNA database.

There are three interesting things to note about these suggestions. To begin with, it is not clear why such a statement would be introduced in a trial. By the time the suspect has become a defendant, a new sample of his DNA should have been tested to establish a full match to the crime-scene sample. At that point, why would the judge or jury care whether defendant is related to a database inhabitant. The relevance of the DNA evidence lies in the full match to the crime-scene sample, and the jury need not consider whether the defendant is a relative of someone not involved in the alleged crime. (One might ask whether the trawl through the database somehow degrades the probative value of the full match, but, if anything, it increases it. [1])

The issue could arise, however, if police were to seek a court order or search warrant to collect a DNA sample from the suspect. At that point, they would need to describe the significance of the partial match to the convicted offender.

This possibility brings us to the second noteworthy point about equation (1). The "odds" (or the corresponding probability) are not the way to present the weight of the partial match. Consider the prior probability of a match in a small database, say, of size N=2. Prior to considering the partial match, why would one think that the probability of a database inhabitant being the sibling of the criminal who resides outside the database is 1/N = 1/2? It is quite improbable that the database of two people includes a relative of every criminal who leaves DNA at a crime-scene. The a priori probability for a small database must be closer to 0 than 1/N.

That the prior probability is less than 1/N is a general result. The only exception occurs when it is absolutely certain that a sibling of the perpetrator is in the database. On that assumption, prior odds of 1 to N-1 are not unreasonable. But that assumption is entirely artificial, and to advise a magistrate that the posterior odds have the value computed according to (1) would be to overstate the implications of the partial match.

The third thing to note about dividing by N is that it accomplishes nothing in producing a viable list of partially matching profiles in a DNA database trawl. The straightforward approach is to produce a short list of candidates in the database whose first-degree relatives might be the source of the crime-scene sample. The minimum value of LR_autosomal x LR_Y-STR should be large enough to keep the two conditional error probabilities (including a candidate when there is no relationship, and not including a candidate when there is a relationship) small. This threshold value does not depend on N. (A later speaker made this observation.)

Equation (1), it seems, is useless. Instead, the magistrate should be told the value of the LR and how often such large LRs would occur when a crime-scene sample comes from a relative versus how often it would occur when it comes from an related person.

Reference

1. David H. Kaye, 2009, Rounding Up the Usual Suspects: A Legal and Logical Analysis of DNA Database Trawls, North Carolina Law Review, 87(2), 425-503.

Prometheus Unbound: Releasing the New Edition of the FJC Reference Manual on Scientific Evidence

Two days ago, the National Academy of Sciences released a third edition of the Federal Judicial Center’s Reference Manual on Scientific Evidence. I listened to the webcast of the unveiling as an insider and an outsider. An insider in that I co-authored two of the chapters. An outsider in that until the Manual eventually emerged, I seemed poised on the exterior side of the event horizon of a singularity into which drafts disappeared and time slowed.

Wednesday's unveiling included remarks from the two co-chairs of the NAS committee assembled to commission and supervise the writing of the manual—a group of five judges and five science professionals (a physician, a toxicologist, an engineer, a statistician, and an epidemiologist). Judge Gladys Kessler explained that in 1993, Daubert v. Merrell Dow Pharmaceuticals established “the gatekeeping role” of federal judges.

Certainly, the majority opinion, penned by Justice Blackmun in Daubert, is famous for this metaphor, but if federal judges were not gatekeepers before 1993, waht were they? Surely not sheep. The Daubert opinion draws heavily on prior case law regarding the Federal Rules of Evidence, substituting for the previously dominant “austere” requirement of general acceptance in the scientific community a multifaceted inquiry into “evidential reliability.” Under either legal standard, however, judges are gatekeepers.

Although Judge Kessler correctly suggested that Daubert’s reliability standard (borrowed from earlier court of appeals cases) goes beyond mere relevancy, the same can be said for the general-acceptance standard (announced in a court of appeals case in 1923) that it displaced. Thus, the notion that judges were not gatekeepers for scientific evidence until 1993 always has struck me as odd. (For more on this legal history and the meaning of Daubert, see Kaye et al. (2011).)

Dr. Jerome Kassirer fielded a number of questions from the virtual and physical audiences. One came from a forensic scientist or analyst in Florida who wanted to know if there were any “practicing forensic scientists” on the editorial committee. The response, that the Manual relied on the very detailed 2009 NRC report on forensic science in its treatment of the forensic sciences, missed the subtext of the question. The practicing forensic science community has been bashing the 2009 report for not accurately depicting the knowledge base of forensic identification techniques (other than DNA evidence). The criticism often takes the form of complaints that the committee lacked enough forensic scientists. (For a rejoinder from the co-chair of that committee, see Edwards (2010).)

Another question was why there was no chapter on digital forensics. The answer referred to the failure of the designated author to produce a manuscript that the committee thought would be useful or intelligible to judges. This probably was not the only chapter to fall by the wayside. Indeed, the problems encountered with such chapters may be part of a more complete answer than the one given to the interlocutor who asked whether an 11-year gap between editions was not a bit much.

A final question to which I alerted included a little speech about the importance of Bayesian inference. The questioner wanted to know why the Manual did not mention Bayes’ rule. Evidently, the questioner was not updating his prior beliefs with any data, for the chapters on statistics, DNA evidence, and medicine have substantial discussions of Bayes' rule. A better question would have been why there is not more discussion in the epidemiology chapter or why the presentation in the medicine chapter is so garbled. But that is a subject for another day.

References

Harry T. Edwards, 2010, The National Academy of Sciences Report on Forensic Sciences: What it Means for the Bench and Bar, Presentation at the Superior Court of the District of Columbia Conference on The Role of the Court in an Age of Developing Science & Technology, Washington, D.C., May 6, available at http://www.fd.org/pdf_lib/The NAS Report on Forensic Science.pdf.

David H. Kaye et al., 2011, The New Wigmore, A Treatise on Evidence: Expert Evidence, 2d ed., New York, NY: Aspen Pub.

National Research Council Committee on the Development of the Third Edition of the
Reference Manual on Scientific Evidence ed., 2011, Reference Manual on Scientific Evidence, Washington DC: National Academies Press.

"The first experimental study exploring DNA interpretation"

A recent study, entitled “Subjectivity and Bias in Forensic DNA Mixture Interpretation,” proudly presents itself as “the first experimental study exploring DNA interpretation.” The researchers are to be commended for seeking to examine, on at least a limited basis, the variations in the judgments of analysts about a complex mixture of DNA.

In addition to documenting such variation, they suggest that their experiment shows that motivational or contextual bias caused analysts in an unnamed case in Georgia to include one suspect in a rape case as a possible contributor to the DNA mixture. This claim merits scrutiny. The experiment is not properly designed to investigate causation, and the investigators' causal inference lacks the foundation of a controlled experiment. To put it unkindly, if an experiment is an intervention that at least attempts to control for potentially confounding variables so as to permit a secure inference of causation, then this is no experiment.

In the study, Itiel Dror, a cognitive neuroscientist and Honorary Research Associate at University College London, and Greg Hampikian, a Professor of Biology and Criminal Justice at Boise State University, presented electropherograms to 17 “expert DNA analysts ... in an accredited government laboratory in North America.” The electropherograms came from a complex mixture of DNA from at least four or five people recovered in a gang rape in Georgia. The article does not state how many analysts worked on the case, whether they worked together or separately, the exact information that they received, or whether they peeked at the suspects’ profiles before determining the alleles that were present in the mixture. They imply that the analysts were told that unless they could corroborate the accusations, no prosecution could succeed. Reasonably enough, Dror and Hampikian postulate that such information could bias an individual performing a highly subjective task.

In the actual case, one man pled guilty and accused three others of participating. The three men denied the accusation. The Georgia laboratory found that one of the three could not be excluded. Contrary to the expectations or desires of the police, the analysts either excluded the other two suspects or were unable to reach a conclusion as to them.

The 17 independent analysts shown the electropherograms from the case split on the interpretation of the complex mixture data. The study does not state the analysts’ conclusions for suspects 1 and 2. Presumably, they were consistent with one another and with the Georgia laboratory’s findings. With regard to suspect 3, however, “One examiner concluded that the suspect ‘cannot be excluded’, 4 examiners concluded ‘inconclusive’, and 12 examiners concluded ‘exclude.’”

From these outcomes, the researchers draw two main conclusions. The first is that “even using the ‘gold standard’ DNA, different examiners reach conflicting conclusions based on identical evidentiary data.”

That complex mixture analysis is unreliable (in the technical sense of being subject to considerable inter-examiner variation) is not news to forensic scientists and lawyers. Although the article implies that the NRC report on forensic science presents all DNA analysis as highly objective, the report refers to “interpretational ambiguities,” “the chance of misinterpretation,” and “inexperience in interpreting mixtures” as potential problems (NRC Report 2009, 132). The Federal Judicial Center’s Reference Manual on Scientific Evidence (Kaye & Sensabaugh 2011) explains that “A good deal of judgment can go into the determination of which peaks are real, which are artifacts, which are ‘masked,’ and which are absent for some other reason.” In The Double Helix and the Law of Evidence (2010, 208), I wrote that “As concurrently conducted ... , most mixture analyses involving partial or ambiguous profiles entail considerable subjectivity.” In 2003, Bill Thompson and his colleagues emphasized the risk of misinterpretation in an article for the defense bar.

These concerns about ambiguity and subjectivity have not escaped the attention of the courts. Supreme Court Justice Samuel Alito, quoting a law review article and a book for litigators, wrote that

[F]orensic samples often constitute a mixture of multiple persons, such that it is not clear whose profile is whose, or even how many profiles are in the sample at all. All of these factors make DNA testing in the forensic context far more subjective than simply reporting test results … .

and that

STR analyses are plagued by issues of suboptimal samples, equipment malfunctions and human error, just as any other type of forensic DNA test.

District Attorney’s Office for Third Judicial Dist. v. Osborne, 557 U.S. __ (2009) (Alito, J., concurring). Dror and Hampikian even quote DNA expert Peter Gill as saying that “If you show 10 colleagues a mixture, you will probably end up with 10 different answers.” Learning that 17 examiners were unanimous as to the presence of two profiles in a complex mixtures and that they disagreed as to a third supports the widespread recognition that complex mixtures are open to interpretation, and it adds some more information about just how frequently analysts might differ in evaluating one set of electropherograms.

The second conclusion that the authors draw is that in the Georgia case “the extraneous context appears to have influenced the interpretation of the DNA mixture.” This conclusion may well be true; however, it is all but impossible to draw on the basis of this “first experimental study studying DNA interpretation.” As noted at the outset, the “experimental study” has no treatment group. The study resembles collaborative exercises in DNA interpretation that have been done over the years. A true experiment—or at least a controlled one—would have included some analysts exposed to potentially biasing extraneous information. Their decisions could have been compared to those of the unexposed analysts.

Instead of controlling for confounding variables, the researchers compare the outcomes in their survey of analysts’ performance on an abstract exercise to the outcomes for one or two analysts in the original case. This approach does not permit them to exclude even the most obvious rival hypotheses. Perhaps it was not information about the police theory of the case and the prosecution's needs, but a difference in the labs' protocols that caused the difference. Perhaps the examiners outside of Georgia, who knew they were being studied, were more cautious in their judgments. Or, perhaps the police pressure, desires, or expectations really did have the hypothesized effect in Georgia. The study cannot distinguish among these and other possibilities.

In addition, the difference in outcomes between the Georgia group and the subjects in the study seems to be within the range of unbiased inter-examiner variability. How can one conclude that the Georgia analysts would not have included suspect 3 if they had not received the extraneous information and had followed the same protocol as the other 17? If the variability due to ordinary subjectivity in the process is such that 1 time out 17 an analyst will include the reference profile in question, then the probability that a Georgia analyst would do so is 0.059. I am not a firm believer in hypothesis testing at the 0.05 level, but I cannot help thinking that even under the hypothesis that the Georgia group was not affected to the slightest degree by the extraneous information, the chance that the result would have been the same is not negligible.

In raising these concerns, I certainly am not claiming that an expectation or motivation effect arising from information about the nature of the crime and the need for incriminating evidence played no role in the Georgia case. But the research reported in the paper does not go very far to establish that it was a significant factor and that it was the cause of the disparity between the Georgia analysts and the 17 others.

The authors’ caveat that “it is always hard to draw scientific conclusions when dealing with methodologies involving real casework” is not responsive to these criticisms. The problem lies with conclusions that outstrip the data when it would have been straightforward to collect better data. The sample size here does not give a reliable estimate of variability in judgments of examiners working in the same laboratory. The sampling plan ignores the possibility of greater variability across laboratories. Perhaps the confined scope of the study reflects a lack of funding or an unwillingness of forensic analysts to cooperate in research because of the pressure of their caseloads or for other reasons -- a complaint aired in Mnookin et al. (2011). Inasmuch as the researchers do not explain how they chose their small sample, it is hard to know.

Beyond the ubiquitous issue of sample size, the subjects in the "experiment" were not assigned to treatment and control groups. No analysts were given the same extraneous information that the Georgia ones had. Of course, extraneous information presented in an experiment could be less influential than it would be in practice. External validity is always a problem with experiments. But there is reason to believe that a controlled experiment could detect an effect in a case like this. Bill Thompson (2009) reported anecdotes suggesting that even outside of actual casework, different DNA examiners presented with electropherograms of mixtures can be induced to reach different conclusions when given extraneous and unnecessary information about the case. That the effect might be less in simulated conditions does not mean that it is undetectable in a controlled experiment.

Convincing scientific knowledge flows from a combination of well designed experimental and observational studies. Dr. Dror's work on fingerprint comparisons (e.g., Dror 2006) has contributed to a better understanding of the effect of examiner expectations in that task. Experiments designed to detect the impact of potentially biasing information on interpretation of DNA profiles in a controlled setting also would be worth undertaking.

References

Itiel E. Dror & Greg Hampikian (2011), Subjectivity and Bias in Forensic DNA Mixture Interpretation, Sci. & Justice, doi:10.1016/j.scijus.2011.08.004, http://www.scienceandjusticejournal.com/article/S1355-0306%2811%2900096-7/abstract

Itiel E. Dror, David Charlton & Ailsa E. Peron (2006), Contextual Information Renders Experts Vulnerable to Making Erroneous Identifications, Forensic Science International, 156(1): 74-78

David H. Kaye (2010), The Double Helix and the Law of Evidence

David H. Kaye & George Sensabaugh (2011), Reference Guide on DNA Identification Evidence, in Reference Manual on Scientific Evidence, 3d ed.

Jennifer L. Mnookin et al. (2011), The Need for a Research Culture in the Forensic Sciences, UCLA Law Review, 58(3): 725-779

National Research Council Committee on Identifying the Needs of the Forensic Sciences Community (2009), Strengthening Forensic Science in the United States: A Path Forward, Wash DC: National Academy Press

William C. Thompson, Simon Ford, Travis Doom, Michael Raymer, Dan E. Krane, Evaluating Forensic DNA Evidence: Essential Elements of a Competent Defense Review, The Champion, Apr. 2003, at 16

William C. Thompson (2009), Painting the Target Around the Matching Profile: the Texas Sharpshooter Fallacy in Forensic DNA Interpretation, Law, Probability & Risk 8: 257-276

Cross-posted at the Double Helix Law blog

The Expected Value Fallacy in State v. Wright

In State v. Wright, 253 P.3d 838 (Mont. 2011), a woman (identified by the Montana Supreme court as Sierra) complained that her date raped her. No semen was recovered, but a penile swab from Timothy Wright, the man she accused, showed a mixture of DNA. Predictably, the major profile seemed to be the defendant's (presumably coming from his skin cells). The minor profile, however, matched Sierra's, confirming her accusation. The random-match probability was "1 in 467,700 Caucasians" and less for other groups. Id. at 841. The direct examination of the state's DNA analyst included the following colloquy:

Q. When you're determining whether or not [Sierra's] DNA is on that penis, tell me what the language "cannot be excluded" means?
A. So that means that the 16 locations we looked at for a DNA profile was at every of those 16 locations.
Q. So whose DNA is on that penis, that penile swab that you examined at the Lab?
A. Well, it--Timothy Wright and [Sierra] can't be excluded as contributing to that profile.
Q. If you--if you're finding her DNA, how come your conclusion isn't that she's included in the profile? That confuses me.
A. At the Forensic Science Division we don't use the word "included." Instead we use "cannot be excluded." It basically means the same thing. It's just our terminology we use.

Id. The prosecutor pressed on, eliciting the statement that the woman's DNA was present in the penile swab:

Q. Can you explain--let's focus on the Caucasian statistic. Can you explain that statistic to the jury? What's it really mean?
A. So that means that in a population of 467,000 you would expect that one person in that population could be included in this mixture.
Q. All right. How many--what's the population of the state of Montana, do you know?
A. It's approximately a million, just under.
Q. So in this particular scenario we've got a mixture of two DNA's, right?
A. Yes.
Q. Statistically speaking, then, I'm just--I want to make sure I understand you, is there only--are there only two people in the state of Montana that can contribute those particular profiles?
A. Yes. Statistically looking at the state of--or the population of Montana two people in Montana would contribute to this mixture.
Q. Those being whom [sic] according to your test results?
A. According to the test results Timothy Wright and [Sierra].

Id. at 841-42.

The prosecution argued in closing that the woman was included as the contributor and that this meant her DNA was on the defendant. On appeal, the defense contended that the source attribution was a knowingly false statement by the prosecutor.

The Montana Supreme Court concluded that this contention was unfounded, but it also described the analyst's source attribution as "internally inconsistent" with the statements that the defendant "cannot be excluded as a contributor." However, there is no logical inconsistency in this testimony. A test that does not exclude someone includes that person. It may include other people when they are tested--or it may not. If the random match probability is small enough, then the test would be expected to exclude all unrelated people, leaving the defendant (or a twin brother or perhaps a close relative) as the only possible source of the semen.

The actual problem in the case was not that the prosecutor knowingly misrepresented the testimony or deliberately elicited false testimony. It was the analyst erred when the stated that "two people in Montana would contribute to this mixture . . . Timothy Wright and [Sierra]" solely on the basis of the "the test results." The expert apparently reasoned that (1) Montana's population is about 1,000,000; (2) about 500,000 would be women; (3) the exact number of women in Montana with the minor profile is 1 (the random-match probability 1/500,000 times the female population of 500,000); hence, it is practically certain that no one but Sierra contributed the minor profile.

Technically, the quantity 1 is an expected value of a variable X that represents the number of women with the minor profile in a randomly generated population of 500,000 women. Expected values are all around us. If we flip a fair coin twice, the expected number of heads is (1/2) x 2 = 1. But we know quite well that the actual outcomes can vary about the expected value. Thus, the probability that two flips of the coin will produce 2 heads is 1/4. Over many coin flips, this "unexpected value" is expected to occur about 25% of the time. Betting on exactly one head in this situation would produce many losses.

How risky was the analyst's source attribution in Wright? The number of occurrences of the minor profile in the population is analogous to the number of heads that would occur when flipping a very heavily weighted coin 500,000 times. Imagine that we generate many populations of 500,000 profiles from a coin that has a probability of only 1/500,000 on each toss. Some populations will have 0 heads (minor profiles), some will have exactly 1, some will have 2, and so on. The number of heads, X, is approximately a Poisson random variable with mean λ = (1/500,000) x 500,000 = 1. Its probability distribution is f(x; λ) = λ^xe^-λ/x! = e^-1/x! = .368/x! For example f(0; 1) = .368/0! =.368, and f(1; 1) = .368/1! = 0.368.

What is the probability that the analyst is wrong in thinking that there is only 1 woman with the minor profile? Of the many populations we generated with the coin, we can ignore some 36.8% of them--the ones with 0 minor profiles. We can ignore them because the real population has one woman (Sierra)--and possibly more with the minor profile. This leaves 63.2% of the populations to consider.

The analyst will be wrong in asserting X = 1 when we have a population in which X = 2 or more. This situation occurs in every population for which X is not 0 or 1. There are 100% x 36.8% x 36.8% = 26.4% such populations, and all of them are within the 63.2% that apply to this case. Consequently, looking at the DNA evidence in isolation, we conclude that there are 26.4/63.2 = 41.8% possible populations for which the analyst errs in asserting that the minor profile from the swab is Sierra's.

Yet, the jury was informed that the DNA test proved that Sierra's DNA was on the swab. The legal issue on appeal should have been whether this extravagant testimony to which no objection was raised was plain error or offended due process. Cf. McDaniel v. Brown, 130 S. Ct. 665 (2010) (not reaching the due process issue). But regardless of how those issues might be resolved, a well trained DNA analyst should not have testified in this fashion. It is hardly news to the forensic science community that the expected number of DNA profiles in a population must be much less than 1 to strongly support an inference that the profile is unique within that population. See David J. Balding, Weight-of-Evidence for Forensic DNA Profiles 148 (2005) (describing the kind of reasoning employed in Wright as a "uniqueness fallacy"); see also Ian W. Evett & Bruce S. Weir, Interpreting DNA Evidence (1998).

Cross-posted from the Double Helix Law blog.

A Kiss is Just a Kiss: Lip Print Identification in the Criminal Law Bulletin

A periodical for lawyers, the Criminal Law Bulletin, recently published an article on “The Investigative and Evidential Uses of Cheiloscopy (Lip Prints).” [1] The author argues that “concerns about the reliability of lip prints evidence are unfounded” and “that lip prints evidence is admissible evidence.” The legal analysis rests on misconceptions about American and English law, but I won’t spell these out. Instead, I want to comment on the author’s approach to the validation of a technique for scientific identification.

According to the article, the following facts apparently demonstrate that “[c]heiloscopy has a scientific foundation”:

• “Human lips are made up of wrinkles and grooves, just like fingerprints and footprints. Grooves are of several types and these groove types and wrinkles form the lip pattern which is believed to be unique to every individual.”


• A 1970 article in the Journal of the Indian Dental Association reported that “none of the lip prints from the 280 Japanese individuals showed the same pattern.”


• In a 2000 article in the same journal, “Vahanwala and Parekh studied the lip prints of 100 Indians (50 males and 50 females) and concluded that lip prints are unique to individuals” and that “It can therefore be conclusively said — Yes, lip prints are characteristic of an individual and behold a potential to be recognized as a mark of identification like the fingerprint!”


• "Saraswathi et al. studied 100 individuals, made up of 50 males and 50 females, aged 18 - 30, and found that ‘no individual had single type of lip print in all the four compartments and no two or more individuals had similar type of lip print pattern.’"


• “A study by Sharma et al [published, as was the previous study, in the Taiwanese Journal of Dental Sciences] also found that lip prints are unique to every individual.”


• Tsuchisashi studied 1364 Japanese individuals, 757 males and 607 females, aged 3 - 60 years and found no identical lip prints. . . . [T]he lips of the twins frequently showed patterns extremely similar to those of their parents [but nonetheless distinguishable].”

These studies do not address the relevant questions. The hypothesis that lip prints are unique is neither a necessary nor a sufficient condition for forensic utility. Before a method of identification can be considered valid, research should establish that multiple impressions from the same person are typically closer to one another than two impressions from different individuals [2] and that they so much closer that an examiner can accurately classify pairs according to their source. Until these questions are asked and answered, the caution expressed in an article not mentioned in the Criminal Law Bulletin seems apt: “Although lip print identification has been utilized in the court of law in isolated cases, more research needs to be conducted in this field . . . .” [3]

References

1. Norbert Ebisike, The Investigative and Evidential Uses of Cheiloscopy (Lip Prints), 47 Crim. Law Bull. No. 4, Art. 4 (Summer 2011)

2. David H. Kaye, Questioning a Courtroom Proof of the Uniqueness of Fingerprints, 71 Int’l Stat. Rev. 521 (2003), available at http://ssrn.com/abstract=944365

2. Shilpa Patel, Ish Paul, Madhu Sudan Astekar, Gayathri Ramesh, Sowmya G V, A Study of Lip Prints in Relation to Gender, Family and Blood Group, 1 J. Oral & Maxillofacial Pathology No. 1 (2010), abstract available at http://journalgateway.com/index.php/ijomp/article/view/V.1.I.1.Art1

The Transposition Fallacy in Matrixx Initiatives, Inc. v. Siracusano: Part II

The previous posting promised a simple example that would demonstrate the fallacy in claims such this one:

For a p-value of .09, the odds of observing the AER [adverse event report] is 91 percent divided by 9 percent. Put differently, there are 10-to-1 odds that the adverse effect is “real” (or about a 1 in 10 chance that it is not).

Brief of Amici Curiae Statistics Experts Professors Deirdre N. McCloskey and Stephen T. Ziliak in Support of Respondents, Matrixx Initiatives, Inc. v. Siracusano, 131 S.Ct. 1309 (2011) (No. 09-1156).

Here is one such example. A bag contains 100 coins. One of them is a trick coin with tails on both sides; the other 99 are biased coins that have a 0.3 chance of coming up tails and a 0.7 chance of coming up heads. I pick one of these coins at random and flip it twice, obtaining two tails. On the basis of only this sample data (the two tails), you must decide which type of coin I picked. The p-value with respect to the “null hypothesis” (N) that the coin is a normal (albeit biased) heads-tails one is the probability of seeing two tails in the two tosses: p = 0.3 x 0.3 = 0.09. Should you reject the null hypothesis N and conclude that I flipped the unique tails-tails coin? Are the odds for this alternative hypothesis (A) 10:1, as the brief of the statistical experts asserts?

Of course not. Just consider repeating this game over and over. Ninety-nine percent of the time, you would expect me to pick a heads-tails coin. In 9% of those cases, you expect me to get tails-tails on the two tosses (9% x 99% = 8.91%). The other way to get tails-tails on the tosses is to pick the tails-tails coin. You expect this to happen about 1% of the time. Thus, the odds of the tails-tails coin given the data on the outcome of the tosses are 1% to 8.91% = 1:8.91, which is about 1:9. Despite the allegedly significant (in “practical, human, or economic” terms) p-value of 0.09, the alternative hypothesis remains improbable.

A more formal derivation uses Bayes' rule for computing posterior odds. Let tt be the event that the coin I picked produced the two tails when tossed (the data), and let "|" stand for "given that" or "conditioned on." Then Bayes' rule reveals that

Odds(A|tt) = L x Odds(A),
where L is the "likelihood ratio" given by P(tt|A) / P(tt|N) and Odds(A) are the odds prior to flipping the coin. The value of L is 1/.09 = 100/9. Hence,

Odds(A|tt) = (100/9) Odds(A).
Because there is only 1 trick coin and 99 normal coins in the bag, the prior odds of A are Odds(A) = 1:99. Hence, the posterior odds are Odds(A|tt) = (100/9)(1/99) = 100/891 = 1:8.91. In other words, the odds for the alternative hypothesis are only about 1:9 -- practically the opposite of the 10:1 odds quoted in the statistics experts' brief.

The lesson of this example is not that a statistic with a p-value of 0.9 always can be safely ignored. It is that the p-value, by itself, cannot be converted into a probability that the alternative hypothesis is true (“that the adverse effect is ‘real’”). Knowing that the two tails arise only 9% of the time when the head-tails coin is the cause does not imply that 9% is the probability that a heads-tails coin is the cause or that 91% is the probability that the tails-tails coin is the “real” cause. Statisticians have warned against this confusion of a p-value with a posterior probability time and again. The brief of "Amici Curiae Statistics Experts" thus brings to mind the old remark, "With friends like these, who needs enemies?" A more complete review of the brief is available at Nathan Schachtman's website (see Further Readings).

Further Reading

David H. Kaye et al., The New Wigmore, A Treatise on Evidence: Expert Evidence (2d ed. 2011).

Nathan A. Schachtman, The Matrixx Oversold, Apr. 4, 2011, http://schachtmanlaw.com/the-matrixx-oversold/

The Transposition Fallacy in Matrixx Initiatives, Inc. v. Siracusano: Part I

One might expect to hear phrases like “Not statistical significance there!” and “There is no way that anybody would tell you that these ten cases are statistically significant” hurled by a disgruntled professor at an underperforming statistics student. Yet, in January 2011, they came from the Supreme Court bench during the argument in Matrixx Initiatives, Inc. v. Siracusano.[1]

The issue before the Court was “[w]hether a plaintiff can state a claim under § 10(b) of the Securities Exchange Act and SEC Rule 10b-5 based on a pharmaceutical company's nondisclosure of adverse event reports even though the reports are not alleged to be statistically significant.” [2] In the case, the manufacturer of the Zicam nasal spray for colds issued reassuring press releases at a time when it was receiving case reports from physicians of loss of smell (anosmia) in Zicam users. The pharmaceutical company, Matrixx Initiatives, succeeded in getting a security fraud class action dismissed on the ground that the plaintiffs failed to plead “statistical significance.”

Because case reports are just a series of anecdotes, it is not immediately obvious how they could be statistically significant, but a determined statistician could compare the number of reports in the relevant time period to the number that would be expected under some model of the world in which Zicam is neither a cause nor a correlate of anosmia. If the observed number departed from the expected number by a large enough amount—one that would occur no more than about 5% of the time when the assumption of no association is true (along with all the other features of the model)—then the observed number would be statistically significant at the 0.05 level.

The Court rejected any rule that would require securities-fraud plaintiffs to engage in such statistical modeling or computation before filing a complaint. This result makes sense because a reasonable investor might want to know about case reports that do not cross the line for significance. Such anecdotal evidence could be an impetus for further research, FDA action, or product liability claims—any of which could affect the value of the stock. In rejecting a bright-line rule of p < 0.05, the Court made several peculiar statements about statistical significance and the design of studies, but these are not my subject for today. (An older posting, on March 25, has some comments on this issue.)

Instead, I want to look at a small part of an amicus brief from “statistics experts” filed on behalf of the plaintiffs. There is much in this brief, which really comes from two economists (or perhaps these eclectic scholars should be designated historians or philosophers of economics and statistics), with which I would agree (for whatever my agreement is worth). But I was shocked to find the following text in the “Brief of Amici Curiae Statistics Experts Professors Deirdre N. McCloskey and Stephen T. Ziliak in Support of Respondents”:

The 5 percent significance rule insists on 19 to 1 odds that the measured effect is real.²⁶ There is, however, a practical need to keep wide latitude in the odds of uncovering a real effect, which would therefore eschew any bright-line standard of significance. Suppose that a p-value for a particular test comes in at 9 percent. Should this p-value be considered “insignificant” in practical, human, or economic terms? We respectfully answer, “No.” For a p-value of .09, the odds of observing the AER [adverse event report] is 91 percent divided by 9 percent. Put differently, there are 10-to-1 odds that the adverse effect is “real” (or about a 1 in 10 chance that it is not). Odds of 10-to-1 certainly deserve the attention of responsible parties if the effect in question is a terrible event. Sometimes odds as low as, say, 1.5-to-1 might be relevant.²⁷ For example, in the case of the Space Shuttle Challenger disaster, the odds were thought to be extremely low that its O-rings would fail. Moreover, the Vioxx matter discussed above provides an additional example. There, the p-value in question was roughly 0.2,²⁸ which equates to odds of 4 to 1 that the measured effect — that is, that Vioxx resulted in increased risk of heart-related adverse events — was real. The study in question rejected these odds as insignificant, a decision that was proven to be incorrect.

26. At a 5 percent p-value, the probability that the measured effect is “real” is 95 percent, whereas the probability that it is false is 5 percent. Therefore, 95 / 5 equals 19, meaning that the odds of finding a “real” effect are 19 to 1.

27. Odds of 1.5 to 1 correspond to a p-value of 0.4. That is, the odds of the measured effect being real would be 0.6 / 0.4, or 1.5 to 1.

28. Lisse et al., supra note 14, at 543-44.

Why is this explanation out of whack? The fundamental problem is that, within the framework of classical (Neyman-Pearson) hypothesis testing, hypotheses like “the adverse effect is real” or “a measured effect being real” do not have odds or probabilities attached to them. In Bayesian inference, statements like “the probability that the measured effect is ‘real’ is 95 percent, whereas the probability that it is false is 5 percent” are meaningful, but frequentist p-values play no role in that framework. Equating the p-value with the probability that a null hypothesis is true and regarding the complement of a p-value as the probability that the alternative hypothesis is true (that something is “real”) is known as the transposition fallacy. [2] That two “statistics experts” would rely on this crude reasoning to make an otherwise reasonable point is depressing.

The preceding paragraph is a little technical. Soon, I shall post a simple example that should make the point more concretely and with less jargon.

References

1. Transcript of Oral Argument, Matrixx Initiatives, Inc. v. Siracusano, 131 S.Ct. 1309 (2011) (No. 09-1156), 2011 WL 65028, at *12 & *16 (Kagan, J.).

2. Petition for Writ of Certiorari at i, Matrixx Initiatives, Inc. v. Siracusano, 131 S.Ct. 1309 (2011) (No. 09-1156), 2010 WL 1063936.

3. David H. Kaye, David E. Bernstein & Jennifer L. Mnookin, The New Wigmore: A Treatise on Evidence: Expert Evidence (2d ed. 2011).