In research domains where true effect sizes are small (Cohen’s h or d in the range of 0.1–0.3), the difference between a significant and non-significant result often hinges on analytic decisions that are invisible in a published summary: which trials were included, how flawed sessions were classified, whether chronological ordering of studies was preserved. Berger’s approach, procuring unpublished dissertations and comparing them line-by-line against published counterparts, is a form of data provenance verification that is rarely attempted but is especially consequential in small-effect domains where publication bias and selective reporting have outsized leverage.¹

Berger’s audit of the Blackmore corpus documented several categories of discrepancy between the unpublished dissertation and the published papers: (1) published reports did not veridically reflect the original data; (2) flaws were invoked selectively, significant results were dismissed by citing methodological problems, while non-significant results from studies Blackmore herself acknowledged as flawed in the dissertation were published without equivalent caveats; (3) admittedly flawed experiments were mixed with supposedly unflawed studies in published summaries without segregation, creating a misleading impression of methodological uniformity; (4) the chronological ordering of studies was reordered in at least two instances, potentially affecting how readers interpreted the trajectory of the research program. Berger concluded that no conclusions, for or against psi, could be drawn from the database as a whole, because the vast majority of the studies were, by Blackmore’s own assessment in the dissertation, individually flawed.¹

One of the most methodologically significant findings in the Blackmore audit was the asymmetric application of quality criteria: the same categories of procedural flaw were used to dismiss studies that produced significant results, but were not applied to dismiss studies that produced non-significant results. This asymmetry, what Berger characterized as a double standard in evaluating extraordinary claims, is a specific form of confirmation bias in analytic reporting.¹ The artifact it produces is a database that appears to show consistent null results not because the experiments were uniformly well-conducted and uniformly non-significant, but because the reporting framework filtered out significant results via flaw-invocation while passing through non-significant results from equally flawed studies. Under the editorial standard adopted by ESP-Nexus (the C28 evidence-quality doctrine, which treats results from methodologically broken studies as carrying zero weight in either direction), the corpus contributes no decisive evidence in either direction: the Blackmore corpus, as audited, supports neither a pro-psi nor an anti-psi conclusion.¹

In small-effect literatures, implausibly large effect sizes are a diagnostic signal for methodological problems, optional stopping, selective trial inclusion, undisclosed analytic flexibility, or outright data irregularities. The Spinelli dissertation reported ESP effects of a magnitude that fell well outside the range of the broader ganzfeld and forced-choice literature. Berger’s audit documented specific procedural and analytic problems in the dissertation that were consistent with the implausibility of the reported effects.² Under the same C28 evidence-quality doctrine (methodologically broken studies carry zero evidential weight), the documented flaws mean the Spinelli data yields no conclusion in either direction, neither confirming nor disconfirming psi, because the methodological problems are sufficient to explain the reported results without invoking any anomalous process.

Bierman, Broughton, and Berger found that while the PRL autoganzfeld’s hardware RNG-based target selection procedure was sound in principle, using a noise-based generator that excluded sequential dependencies, the resulting target sequence contained a peculiar empirical anomaly: targets numbered 77, 78, 79, and 80 were over-represented, producing a strong over-representation of Set 20 (which contained those four targets). This distributional skew could not be explained by the selection procedure itself. The authors applied a conservative post-hoc correction for response bias and found a slight reduction in overall statistical significance and a weakening of the conclusion that dynamic targets were superior to static targets. Critically, however, the documented target-frequency anomaly could not account for the overall hit excess reported in the PRL autoganzfeld series, meaning the anomaly partially mitigated but did not explain away the positive results.³ The specific artifact addressed was response-bias confounding target-frequency imbalance; the specific control was a post-hoc correction adjusting hit probability for the observed distributional skew; the strength of ruling-out was partial, the correction reduced effect size estimates but left a residual excess of hits unexplained by the artifact.

A key conceptual contribution of the 1998 paper was the formal distinction between two levels of randomization quality: (1) the procedure level, whether the algorithm or hardware generator is theoretically sound and excludes sequential dependencies, and (2) the sequence level, whether the empirically realized sequence of targets, even from a sound procedure, happens to contain distributional anomalies that could interact with subject response biases. A hardware RNG can be procedurally valid while still producing, by chance, a sequence that over-represents certain targets. The paper provided post-hoc correction methods applicable when a closed-deck (balanced) design was not used, and noted that such corrections are unnecessary when the design is balanced.³

The file-drawer problem in parapsychology is typically framed as a concern about suppressed null results inflating apparent effect sizes in meta-analyses. Berger’s audits add a second dimension: even the null results that are published may not accurately represent the underlying data if published reports diverge from source materials. The Blackmore audit demonstrated this concretely, a corpus of null results that had been widely cited as a replication failure turned out, on source-level examination, to be methodologically too compromised to serve as evidence in either direction.¹ This reframes the replication debate: the question is not only whether positive results replicate, but whether the null results used as the comparison baseline are themselves methodologically sound. A null result from a broken study, under the C28 evidence-quality doctrine, carries zero evidential weight against the hypothesis, just as a positive result from a broken study carries zero weight for it.

Berger’s audits were conducted in an era before data-sharing mandates, preregistration infrastructure, or open-science norms in parapsychology. The specific artifacts he documented, discrepancies between dissertation and published data, asymmetric flaw invocation, target-frequency distributional anomalies, are addressable in principle by modern open-science practices: preregistered analysis plans, public data repositories, and independent data audits prior to publication. Whether the broader ganzfeld and forced-choice literatures contain additional source-level discrepancies of the kind Berger documented in the Blackmore corpus remains an open empirical question that would require systematic dissertation-to-publication comparison studies to answer.¹