Snap Shot
- The question: How can an attorney, without training in statistics, test whether a research claim offered in court means what it is said to mean?
- What the research shows: Most misleading research claims are not fabricated. They come from numbers stripped of their definitions, relative figures presented without absolute ones, base rates left out, samples that differ from the person before the court, small or unreplicated findings, and conclusions that go further than the design allows. A short set of questions catches most of these problems, and restating percentages as counts (“4 out of 100”) makes many of them visible.
- What it does not show: These questions identify weaknesses; they do not decide whether a study is right. Every study has limits, and a limitation is not a refutation. No checklist replaces reading the study itself or consulting someone who can.
- The law: Daubert, Joiner, and Kumho direct courts to testing, peer review, error rates, standards, and general acceptance, and to the fit between data and opinion; amended Rule 702 (2023) makes the proponent show reliability by a preponderance. The same framework governs courts-martial (Houser, Griffin) and Arizona courts (Ariz. R. Evid. 702). Learned treatises may be used on cross-examination under Rule 803(18).
- Issues for each side: The same questions apply to every expert. Prosecutors and defense counsel should apply them to their own experts’ studies before trial, not only to the other side’s.
Expert testimony about sexual offending, child abuse, memory, intimate partner violence, alcohol, and risk rests on research, and the research reaches the courtroom in compressed form: a percentage, a “study found,” a risk category, a claim that some behavior is common or rare. Attorneys are expected to test that testimony, and judges are expected to decide whether it is reliable enough to be heard, usually without formal training in research methods. The gap between what a study found and what a witness says it found is where much of the misleading testimony in these cases lives.
The problem is rarely fraud. A figure can be accurate and still mislead if its definition is left out, if it is a relative change presented without the absolute numbers, if it describes a group unlike the person before the court, or if it rests on so few cases that it would likely change with the next study. Several widely read books by scientists and statisticians describe these patterns for general readers: Gigerenzer (2002) on how risks are communicated and misunderstood, including in courtrooms; Ritchie (2020) on why published findings fail to replicate; Bergstrom and West (2020) on misleading numbers, selection effects, and causal claims; Goldacre (2010) on how evidence is distorted between the study and the public; and the chapters collected by Lilienfeld, Lynn, and Lohr (2015) on distinguishing science from pseudoscience in clinical psychology.
This paper draws on those works to set out eight questions an attorney can ask of any research claim. Each is illustrated with studies discussed in the topic papers on this site, chosen because they are familiar to practitioners, not because they are weaker than others; many are strong studies whose findings are routinely stretched by the people citing them. The paper then describes how the questions map onto the legal standards for expert testimony.
What Exactly Was Counted?
Every number in a study rests on a definition, and the definition is usually narrower than the words used to describe it. Bergstrom and West (2020, Chapter 5) describe how numbers acquire a false authority once separated from what was measured. Recidivism is the clearest example in sexual offense cases. “Recidivism” may mean a new arrest, charge, conviction, or self-report; it may count any offense or only a sexual one; and it covers a fixed follow-up period. When the U.S. Sentencing Commission (2021) reported that 4.3% of federal non-production offenders released or placed on probation in 2015 were rearrested for a sex offense, the figure meant 47 of 1,093 people, rearrested rather than convicted, within three years. Stated that way, it is neither a claim that only 4% will ever reoffend nor a claim that 4% committed new offenses; it is a floor on detected reoffending over a short period.
Outcome categories in abuse investigations work the same way. A study that reports only the share of allegations found to be false, typically about 3% to 6% in the major studies, leaves out the larger share that could not be substantiated, about 44% to 57% in the same studies. Unsubstantiated does not mean false, and false does not mean that every other report was true; the two figures are informative only together. That comparison is set out study by study in “Unfounded Is Not False: Outcome Statistics in Child Sexual Abuse Allegations” in the Child Abuse Allegations resource. The general question for any figure is what event was counted, by whom, using what records, over what period, and out of what total.
How Large Is the Effect, in Absolute Terms?
Relative figures describe change; absolute figures describe size. Gigerenzer (2002, Chapter 5) and Goldacre (2010, Chapter 11) both show how a relative change can sound large while the underlying numbers are small. Gigerenzer’s example is breast cancer screening: over ten years, about 4 of every 1,000 women who were not screened and 3 of every 1,000 who were died of breast cancer. That difference can be described as a 25% reduction in risk or as 1 life saved per 1,000 women screened; both are true, and they leave very different impressions.
The same distinction appears in risk testimony. Hanson and colleagues (2018) found that each year a person with a sexual offense history remained offense-free in the community was associated with about a 12% decrease in the odds of sexual recidivism. That is a relative figure. Its practical meaning depends on the starting point: in the same study, the five-year rate of new sexual offenses fell from 9.1% in the first five years to 4.1% in years five to ten and 2.9% in years ten to fifteen for those still offense-free. An attorney who hears “12% lower each year” should ask what it is 12% of. Gigerenzer (2002, Chapter 4) recommends translating probabilities into natural frequencies, counts out of a concrete reference group (“about 4 of every 100 men like him”), because people reason more accurately with counts than with percentages and conditional probabilities. Format matters even for experts. In a study Gigerenzer describes (2002, Chapter 11), more than 800 forensic psychiatrists and psychologists read the same discharge summaries; those asked for the probability that a patient would be violent gave estimates about 50% higher than those asked how many of 100 similar patients would be violent (Slovic et al., 2000). The same chapter discusses Barefoot v. Estelle (1983), in which a psychiatrist who had never examined the defendant testified that he was certain the defendant would be violent in the future. Asking a witness to restate a figure as a count is a simple way to test whether the witness understands it and whether the fact-finder will.
What Is the Base Rate, and What Does a Positive Result Mean?
A test result means little without the base rate, the frequency of the condition in the group being tested. Gigerenzer (2002, Chapter 5) shows with screening examples that when a condition is uncommon, most positive results can be false positives even when the test is fairly accurate, and that physicians, like lay readers, often misjudge this. The questions are how common the condition is in this population, how often the test flags people who have it (sensitivity), and how often it wrongly flags people who do not (specificity).
Screening for autism traits in forensic populations illustrates the point. In a study of darknet CSAM users, half scored at or above the lower cutoff of a brief autism screening questionnaire, but that cutoff’s specificity was only about 46% to 64% (Lätth et al., 2026), so many people without autism also score above it. In London police custody, 5% of arrestees without an existing diagnosis screened positive on a 10-item autism-trait questionnaire (Brown et al., 2025). Neither figure is a rate of autism; both are rates of screening positive, and a positive screen calls for a diagnostic evaluation, not a conclusion. The same reasoning applies to any screen or risk indicator offered against or for a party.
Gigerenzer (2002, Chapters 8–10) also describes two errors that recur in court. The first is confusing the probability of the evidence given innocence with the probability of innocence given the evidence, sometimes called the prosecutor’s fallacy, which most often arises with forensic match statistics. The second is answering the wrong conditional question, as in a defense argument in a murder trial that few men who batter their partners go on to kill them; Gigerenzer (2002, Chapter 8) explains that the relevant question was different, namely how often, when a battered woman has been murdered, the batterer was the killer; using the defense’s own figure and national homicide data, he estimated that about 40 of every 45 such women had been killed by their batterers. Goldacre (2010, Chapter 11) describes a related error in the case of Sally Clark, in which an expert told the jury that the chance of two sudden infant deaths in one family was about 1 in 73 million. The figure was obtained by squaring the estimated chance of one such death, as if the two deaths were independent, and it was widely misread as the probability that the mother was innocent, an instance of the prosecutor’s fallacy. Each example turns on a question attorneys can ask: probability of what, given what? Feelings also shape these judgments. Slovic and colleagues (2005) describe the affect heuristic, the tendency to judge a hazard’s risks and benefits by how one feels about it, which helps explain why a vivid case can outweigh a base rate in the minds of jurors and experts alike.
Who Was Studied, and Compared With Whom?
A finding describes the people who were studied, and the way they came to be studied can shape the result. Bergstrom and West (2020, Chapter 6) devote a chapter to selection effects: when the sample is chosen in a way related to the outcome, patterns can appear that do not exist in the wider population. Forensic and clinical samples are selected by detection, referral, conviction, treatment, or willingness to participate, and each filter matters.
Estimates of undisclosed contact offending among people convicted of CSAM offenses show why. In a meta-analysis, about 1 in 8 online offenders had an officially recorded contact offense, while about half admitted one in the studies with self-report data (Seto et al., 2011). The Butner study’s much higher figure came from men in a voluntary, intensive residential treatment program in which disclosure was expected and polygraph examinations were used (Bourke & Hernandez, 2009), and the federal supervision sample studied by Drury and colleagues (2020) involved disclosures made under supervision conditions that included polygraph testing. These settings may elicit offenses that would otherwise stay hidden, or may produce pressure to over-disclose; the design cannot tell which, and the findings may not describe people outside those settings. In the same way, a study of men seeking help for pedophilic disorder (Abé et al., 2021) or of anonymous darknet volunteers (Lätth et al., 2026) describes those groups, not defendants in general.
The comparison group matters as much as the sample. Goldacre (2010, Chapters 4–5) explains why a fair test needs a comparison and why, without one, improvement can reflect natural recovery, regression to the mean, or expectation rather than the intervention. An evaluation of the UK Stop It Now! prevention campaign found more help-seeking during active campaign periods than inactive ones (Newman et al., 2024), a useful design for a public campaign, but not a randomized comparison. A claim that a behavior is “typical of abuse victims” or “typical of offenders” invites the same question: compared with whom? If the behavior is also common among people who were not abused or did not offend, it does little to distinguish them.
How Much Evidence Does the Finding Rest On, and Has It Held Up?
Ritchie (2020, Chapters 2 and 4) describes how small samples, flexible analysis, and a publication system that favors positive results combine to produce findings that do not replicate. In 2015, a large collaborative project repeated 100 published psychology studies and obtained statistically significant results in only about a third of them (Open Science Collaboration, 2015). The lesson is not that psychology is unreliable; it is that a single study, especially a small one with a surprising result, is a starting point.
Two features deserve particular attention in forensic research. The first is the number of events, not just the number of participants. A recidivism study of 1,000 people with 30 recidivists has, for many purposes, the statistical power of a study of 30. Critics of the research base for one CSAM risk tool pointed to the small numbers of recidivists, missing data, and possibly outdated samples (Scurich & Krauss, 2023), and the tool’s developers agreed that those limitations were real while disputing the conclusion drawn from them (Helmus et al., 2025). A finding that every man who reoffended against a girl had more girl content in his collection rested on 14 men who reoffended (Eke & Seto, 2023); the authors presented it with appropriate caution. The second is how the work was reviewed. A preprint has not been peer reviewed, a survey report from an advocacy or service organization has not ordinarily been reviewed in the way a journal article is, and a meta-analysis is only as good as the studies in it. Peer review is a check, not a guarantee; Ritchie (2020, Chapters 3–6) describes fraud, bias, negligence, and exaggerated press releases that passed through it. The questions are how many cases the finding rests on, whether it has been repeated by independent researchers, and how it was reviewed.
Does the Conclusion Follow From the Design?
Correlation is not causation, but the more common problem in court is subtler: a study designed to answer one question is cited to answer another. Bergstrom and West (2020, Chapter 4) describe how associations are converted into causal claims, and how confounding variables, reverse causation, and chance can produce associations that do not reflect cause. Goldacre (2010, Chapter 10) describes regression to the mean, the tendency of extreme measurements to be followed by less extreme ones, which can make any intervention applied at a low point look effective.
In abuse and offense cases, the design question often concerns what a study can say about a mechanism. Qualitative interviews with autistic men convicted of sexual offenses, or with practitioners who treat them, describe how participants understand their offending; they generate hypotheses about mechanisms but cannot test them, because there is no comparison with autistic people who did not offend or with non-autistic people who did. Risk tools are designed to rank and estimate group recidivism rates, not to determine whether a particular person committed the charged offense. Testimony that moves from “this is associated with” to “this caused,” or from “this predicts group recidivism” to “this shows what he did,” has gone beyond the design.
Is the Claim Testable?
Lilienfeld, Lynn, and Lohr (2015) describe ten warning signs that a claim in clinical psychology is not functioning as science: reliance on anecdotes and testimonials rather than controlled tests; explanations adjusted after the fact so that no result can count against them; claims that evade peer review; a focus on confirming rather than testing; and the absence of self-correction over time. A single warning sign does not make a claim false, and well-established clinical practices sometimes rest on thin evidence, but the signs identify claims that need closer examination.
The test that matters most in court is whether any observation could count against the claim. In the foreword to the same volume, Tavris (2015) describes courtroom testimony in which an expert treated every fact as confirming her diagnosis: the mother’s charm, the child’s loyalty, and other physicians’ findings were each explained as further evidence of it. A claim that is supported by a behavior and also by its opposite (a child who disclosed promptly and a child who delayed; a defendant who showed emotion and one who did not) explains everything and therefore predicts nothing. The same concern applies to frameworks such as “counterfeit deviance,” which is an approach to assessment supported by case material rather than a tested finding, and to any profile offered to show that a person is or is not the kind of person who would offend.
Does It Apply to This Person?
Research describes groups; trials concern individuals. Faigman, Monahan, and Slobogin (2014) call this the problem of group-to-individual (G2i) inference. They distinguish framework evidence, which describes general scientific propositions, from diagnostic evidence, which applies those propositions to a particular case, and argue that courts should analyze fit, error rates, testability, and the other admissibility factors differently for the two. Research can support framework testimony directly; an opinion that a particular person fits or does not fit a pattern requires a separate, individualized basis. A base rate, a risk category, or a finding about a population can be relevant without answering whether this defendant reoffended, whether this child was abused, or whether this witness’s memory is accurate.
The questions above therefore end with fit: how closely the person before the court resembles the people studied in age, sex, offense type, setting, and the way the information was obtained, and what, beyond the group data, the expert relied on to reach an opinion about the individual.
Limits of These Tools
These questions find weaknesses; they do not settle disputes. Every study has limits, authors usually describe them, and an attorney who treats any limitation as fatal invites the response that no research would survive the same standard. The question is whether the limitation affects the specific inference being drawn. A small study can be the best evidence available, and a large study can be poorly suited to the case. Popular books simplify, and the books cited here are guides to reasoning, not authorities on the specific studies discussed in the topic papers. For contested methodological questions, the study itself, the published commentary on it, and qualified consultation remain necessary.
Research Claims and the Law
Federal and Military Standards
Under Daubert v. Merrell Dow Pharmaceuticals, Inc. (1993), a trial court must determine whether expert testimony rests on a reliable foundation and is relevant to the case, considering among other things whether the theory or technique can be and has been tested, whether it has been subjected to peer review and publication, its known or potential error rate, the existence of standards controlling its operation, and its general acceptance. General Electric Co. v. Joiner (1997) held that a court may exclude an opinion when there is too great an analytical gap between the data and the opinion offered, and Kumho Tire Co. v. Carmichael (1999) extended the gatekeeping obligation to all expert testimony, including clinical and experience-based testimony. Federal Rule of Evidence 702, as amended December 1, 2023, requires the proponent to show the court that it is more likely than not that the testimony rests on sufficient facts or data, is the product of reliable principles and methods, and reflects a reliable application of those methods to the case. The questions in this paper correspond closely: what was counted and how large the effect is go to sufficient facts and data; base rates and error rates go to reliability; sample, design, and replication go to method; and fit goes to application.
In courts-martial, United States v. Houser (1993) requires the military judge to consider the expert’s qualifications, the subject matter and basis of the testimony, its legal relevance and reliability, and whether its probative value outweighs other considerations, and United States v. Griffin (1999) applied Daubert to expert testimony under Military Rule of Evidence 702, which tracks the federal rule. Under Rule 803(18) of both the Federal and Military Rules of Evidence, statements in a learned treatise established as a reliable authority may be read into evidence on cross-examination or relied on by an expert on direct, although the treatise itself is not received as an exhibit. Rule 703 permits an expert to rely on facts or data of a kind reasonably relied on in the field, which makes the quality of the underlying studies a proper subject of examination.
Arizona
Arizona amended Rule 702 in 2012 to adopt the federal standard, and Arizona courts apply the Daubert factors in deciding admissibility. In State v. Salazar-Mercado (2014), the Arizona Supreme Court held that general expert testimony about behavioral characteristics may be admitted without the expert having examined the parties, provided it meets Rule 702; the reliability of the research underlying such general testimony is therefore what Rule 702 tests. Arizona Rule of Evidence 803(18) parallels the federal learned-treatise rule.
Special Issues in Legal Practice
The principles described above apply with equal force to every party in a legal proceeding. The science operates the same way regardless of who is asking the questions, and the research summarized here does not by itself favor either side. What differs between the parties is not the science but the vantage point — the particular places where these issues tend to surface, and the particular errors each party is best positioned to guard against. The two summaries below identify those recurring issues. They are offered for orientation, not as litigation strategy; in every case the controlling question is what the evidence in that case will, and will not, support, and the expert’s role is to inform the trier of fact rather than to advocate for either side.
Special Issues for Prosecutors
The questions in this paper support testing defense expert testimony that relies on qualitative or case material as if it established a mechanism, on studies of populations unlike the defendant, on relative risk figures without the absolute rates, or on low observed recidivism rates presented as true rates of reoffending. They also support asking whether a defense framework is testable: if every fact in the record is explained as consistent with the framework, it is not distinguishing anything. Prosecutors can ask defense experts to restate rates as counts, to identify the definition and follow-up period behind every figure, and to say what, beyond group data, supports the opinion about this defendant.
The same questions apply to prosecution testimony. Figures drawn from treatment or polygraph settings, single studies with surprising results, screening results presented as diagnoses, and risk categories presented as predictions about an individual are all open to the same examination. Testimony that a behavior is consistent with abuse or offending should identify how common that behavior is among people who were not abused or did not offend. Testing the prosecution’s own expert with these questions before trial is the most reliable way to avoid an exclusion ruling or an effective cross-examination.
Special Issues for Defense
The questions in this paper support testing prosecution expert testimony that cites outlier figures as typical, relies on samples selected by treatment, supervision, or detection, presents match statistics or risk scores in ways that invert the conditional probability, or moves from group findings to conclusions about the defendant. Defense counsel can ask what was counted, out of what total, over what period; what the base rate is; how many events the finding rests on; whether it has been replicated; and whether the expert’s opinion about this defendant rests on anything beyond group data.
The same questions apply to defense testimony. Observed recidivism rates are floors, not measures of true reoffending; studies showing low rates have their own small samples and limited follow-up; qualitative accounts of how autistic or intellectually disabled people come to offend are hypotheses; and a favorable risk score is a group estimate, not a finding that the defendant poses no risk. Arguing that a limitation in the prosecution’s research is fatal while relying on research with the same limitation is a vulnerability on cross-examination. Applying these questions to defense experts’ studies before trial protects their credibility.
This paper is for educational purposes only and is not legal advice. The author is a psychologist, not an attorney; summaries of law are general and must be verified against current authority or with a licensed attorney.
References
Abé, C., Adebahr, R., Liberg, B., Mannfolk, C., Lebedev, A., Eriksson, J., Långström, N., & Rahm, C. (2021). Brain structure and clinical profile point to neurodevelopmental factors involved in pedophilic disorder. Acta Psychiatrica Scandinavica, 143(4), 363–374. https://doi.org/10.1111/acps.13273
Bergstrom, C. T., & West, J. D. (2020). Calling bullshit: The art of skepticism in a data-driven world. Random House.
Bourke, M. L., & Hernandez, A. E. (2009). The “Butner Study” redux: A report of the incidence of hands-on child victimization by child pornography offenders. Journal of Family Violence, 24(3), 183–191. https://doi.org/10.1007/s10896-008-9219-y
Brown, D., Procyshyn, T. L., Allison, C., Neyroud, E., & Baron-Cohen, S. (2025). Neurodiversity in custody: Screening results for ADHD and autistic traits in individuals arrested by the London Metropolitan Police. Criminal Behaviour and Mental Health, 35, 327–333. https://doi.org/10.1002/cbm.70018
Drury, A. J., Elbert, M. J., & DeLisi, M. (2020). The dark figure of sexual offending: A replication and extension. Behavioral Sciences & the Law, 38(6), 559–570. https://doi.org/10.1002/bsl.2488
Eke, A. W., & Seto, M. C. (2023). Correspondence of child age and gender distribution in child sexual exploitation material and other child content with age and gender of child sexual assault victims. Sexual Abuse, 35(3), 375–397. https://doi.org/10.1177/10790632221108951
Faigman, D. L., Monahan, J., & Slobogin, C. (2014). Group to individual (G2i) inference in scientific expert testimony. University of Chicago Law Review, 81(2), 417–480.
Gigerenzer, G. (2002). Calculated risks: How to know when numbers deceive you. Simon & Schuster.
Goldacre, B. (2010). Bad science: Quacks, hacks, and big pharma flacks. Faber and Faber.
Hanson, R. K., Harris, A. J. R., Letourneau, E., Helmus, L. M., & Thornton, D. (2018). Reductions in risk based on time offense-free in the community: Once a sexual offender, not always a sexual offender. Psychology, Public Policy, and Law, 24(1), 48–63. https://doi.org/10.1037/law0000135
Helmus, L. M., Eke, A. W., & Seto, M. C. (2025). What risk assessment tools can be used with men convicted of child sexual exploitation material offenses? Recommendations from a review of current research. Law and Human Behavior, 49(1), 71–88. https://doi.org/10.1037/lhb0000594
Lätth, J., Joleby, M., McMahan, A., Luke, T. J., & Rahm, C. (2026). Child sexual abuse material users on the darknet: Psychiatric morbidities related to offence behavior. Sexual Abuse, 38(1), 3–22. https://doi.org/10.1177/10790632251347562
Lilienfeld, S. O., Lynn, S. J., & Lohr, J. M. (2015). Science and pseudoscience in clinical psychology: Initial thoughts, reflections, and considerations. In S. O. Lilienfeld, S. J. Lynn, & J. M. Lohr (Eds.), Science and pseudoscience in clinical psychology (2nd ed.). Guilford Press.
Newman, E. F., Efthymiadou, E., Quayle, E., Squire, T., Denis, D., Wortley, R., Beier, K. M., & Koukopoulos, N. (2024). The impact of a public health campaign to deter viewing of child sexual abuse images online: A case study of the UK Stop It Now! campaign. Sexual Abuse, 36(6), 635–661. https://doi.org/10.1177/10790632231205784
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Ritchie, S. (2020). Science fictions: How fraud, bias, negligence, and hype undermine the search for truth. Metropolitan Books.
Scurich, N., & Krauss, D. A. (2023). Risk assessment of child-pornography-exclusive offenders. Law and Human Behavior, 47(4), 499–509. https://doi.org/10.1037/lhb0000537
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Legal Authorities
Barefoot v. Estelle, 463 U.S. 880 (1983).
Daubert v. Merrell Dow Pharmaceuticals, Inc., 509 U.S. 579 (1993).
General Electric Co. v. Joiner, 522 U.S. 136 (1997).
Kumho Tire Co. v. Carmichael, 526 U.S. 137 (1999).
United States v. Griffin, 50 M.J. 278 (C.A.A.F. 1999).
United States v. Houser, 36 M.J. 392 (C.M.A. 1993).
State v. Salazar-Mercado, 234 Ariz. 590, 325 P.3d 996 (2014).
Fed. R. Evid. 702, 703, 803(18).
Mil. R. Evid. 702, 703, 803(18).
Ariz. R. Evid. 702, 803(18).
Related topics from Arizona Forensic Services: Psychosexual Risk Evaluations · Online Sexual Offending · Autism and Online Sexual Offending · Child Abuse Allegations · Counterintuitive Testimony · Memory in the Courtroom · False Confessions · Alcohol Blackouts · Courts-Martial