Executive Summary

Start with why the paper treats this as something worth counting. It leans on two frameworks. Recombinant novelty holds that innovation comes from tying existing elements together in ways that break with convention while staying intelligible. Transformative creativity holds that fundamentally new ideas arrive when the structure of a conceptual space itself changes. Within the first frame, combining datasets in unusual ways had already been measured, but moving data across subjects was an empty space. The analogy the authors reach for is a drug. Aspirin was used against pain and fever before it moved on to cardiovascular prevention, and as the candidate compounds within easy reach run out, that kind of move becomes a way of drawing more value without paying to make something new. On the data side, earlier work had mostly established that having data helps.

Fix the vocabulary first. What this article calls repurposing is the use of an existing dataset in research on a subject different from the one it had been serving. That is the paper's own term, and it is distinct from using the same data once more on the same task. Putting ImageNet back to work on image classification does not count here; pulling ImageNet into an entirely different question does. The problem is how to turn that distance into a number. Reading one paper at a time and judging by hand does not get anyone past ten thousand.

The method chosen by Yulin Yu (College of Information Science, University of Arizona), Yong-Yeol Ahn (School of Data Science, University of Virginia) and Daniel M. Romero (School of Information, University of Michigan) is to use distance in semantic space. For any paper, there are earlier papers that used its dataset at least a year before. Measure how far those earlier papers sit from the focal paper in subject matter, then average with a weight for how much the datasets overlap. The further away, the higher the repurposing score. The preprint went up on arXiv on 15 September 2026 and carries no journal of record yet.

1.1How 12,286 papers were left standing

The raw material is the 16 June 2021 snapshot of Papers with Code. The paper sets out why it chose that source. The snapshot records the datasets a paper actually used for analysis or model training, not the datasets it cited, and the authors attach an earlier observation as the ground for that choice: data citation is frequently omitted and often fails to reflect actual use. Bibliographic records and the citation network come from SciSciNet version 1 and an August 2024 OpenAlex snapshot. The sample narrowed in five steps. From 60,647 raw records, removing the 20,016 that could not be matched to OpenAlex leaves 40,631; of those, 35,801 were published before 2021 with subject tags and references intact. Clearing out the 19,850 with no conference or journal affiliation brings the count to 15,951, and removing the 3,665 papers that never had an opportunity for their dataset to be reused leaves 12,286 papers for analysis. They cover 1,689 datasets, and the corpus runs through major venues including CVPR, ACL and NeurIPS.

That last step has to be carried over precisely, or the 55% further down will be misread. A paper counts as having an opportunity for reuse when one of the datasets it used had already been used more than a year earlier and, at the same time, is shared by some paper more than a year later. Both conditions apply together. So this sample contains no paper whose dataset nobody ever used again. The extreme case of zero diffusion was removed before anything was calculated. This condition is absent from the five limitations the paper numbers for itself, and it becomes necessary again in section 5.

1.2Measuring by distance

The repurposing score multiplies two ingredients. One is semantic similarity. SPECTER2, an embedding model trained on scholarly documents, turns paper titles into vectors, and cosine similarity is taken between them. Titles, not full texts. The other ingredient is dataset overlap, measured as the Jaccard index of the two papers' dataset sets. For every earlier paper the similarity is averaged with overlap as the weight, and the repurposing score is one minus that average. A larger value means the data travelled further. The theoretical range runs from 0 to 2, but the observed range was 0.009 to 0.659. The regressions take the standardised value.

1.3What this ruler cannot measure

The paper raises the limits of its proxy before anyone else can. The heaviest is that the measuring instrument may itself be contaminated. SPECTER2 was trained on citation relationships, so two papers that a later paper cites together end up close in the embedding space. The consequence is that the more influence a repurposing ends up having, the more artificially close to its predecessors it looks, and the lower its score comes out; the diffusion side is inflated by the same mechanism. The authors set out this problem in the main text and then redrew three figures using OpenAI's text-embedding-3-small, which never learned a citation network. The verdict reaches as far as the direction being the same. Nowhere does the paper claim the magnitudes matched.

They also tested whether the score matches human judgement, under conditions. Among datasets used in three to five papers, only the top 30% by within-year score variance were kept, and in each of those datasets the highest- and lowest-scoring papers were paired into 39 pairs. Two people rated them, and one of the two is an author of the paper; the other is a master's student. The two raters agreed with each other 71.2% of the time, the score agreed with human judgement 73.1% of the time, and on the cases where both raters agreed the figure is 82.1%. The paper itself records that this procedure deliberately picks cases with sharp contrast, so accuracy may be overstated for more typical or ambiguous comparisons.

Bias in the sample comes with its own warning from the authors. Papers with Code indexes mostly benchmark-driven work, so performance-centred research is over-represented while theoretical work and empirical work outside benchmarks are likely under-represented. That the inclusion criteria were never clear is written up as the first limitation. The sections below therefore describe not AI research as a whole but a pattern observed in the territory where benchmarks circulate.

Before naming the measure that moved, it helps to unpack what that measure records. The disruption index looks at the shape of the citation network after a paper appears. It counts whether later work cited that paper alone, cited the paper together with the paper's own references, or cited only those references. More of the first raises the value; more of the second lowers it. If the people who come afterwards read this paper instead of the earlier literature, that is disruption; if they read it alongside that literature, that is consolidation. What the index records is not whether a paper is good or bad but whether the citation flow split or carried on.

This study computed the index over a three-year window after publication, and restricted it to papers with at least one citation and at least one reference. The criticism that the index is sensitive to reference counts and citation counts is one the paper raises itself, answering it by entering both counts as controls. The dispute over the index itself is taken up separately further on.

2.1The common summary and the table disagree

The regression ran twice over the same sample of 12,286 papers. Only the dependent variable changed. Disruption was fitted with ordinary least squares and citations with a negative binomial model, and publication year was controlled as a category so that papers are weighed against others from the same year. The paper's main figure lines up the coefficients from twelve models that add controls one at a time, but the only model released as a numeric table is the last one with every control in place. The values in the table below come from it.

arXiv:2609.16736, appendix Tables S1 and S2. Both models have N = 12,286 and are the full specification, controlling for publication year, number of datasets, number of authors, institutional influence and more. Converted to a rate, the citation coefficient is −0.84%, and that conversion is ours.

The two rows must not be flattened into one sentence. The summary that tends to circulate says repurposing research shook the field but drew less attention, and that is not what the table says. A p of 0.412 means there is no evidence of less attention, not that there was less attention. The point estimate leans very slightly negative, and in the fully controlled model it is not significant. The main text of the paper says precisely that. The same paper's Significance Statement, though, writes that most repurposed datasets receive less immediate attention, and the abstract writes that they fail to gain broad visibility in the short term. The three versions are slightly out of step with each other, and this article follows the one that matches the table.

As for why citations did not move, the paper settles on no explanation. The authors put forward earlier work showing that researchers who change direction lose out in the short run, then take it back themselves: repurposing data does not amount to an author-level pivot, so whether that explanation suffices is unclear. The paper's position is that this is not yet known.

2.2What 0.10 is worth on the scale

A tenth of a standard deviation per standard deviation is, on its own, a small effect. It needs something to be weighed against. The paper writes that this effect is comparable in size to the effect of the number of datasets, and that comparison is better left unused. Dataset count went into the model log-transformed but not standardised, so a one-standard-deviation-to-one-standard-deviation comparison does not hold. Only two variables in that table are standardised, and those two are the real scale.

Read from the same column of Table S1 in arXiv:2609.16736. The ratios are our calculation. The novelty coefficient is negative. A sentence that reports only the size, about half, points the wrong way.

The most honest scale is the first row. Unusualness of dataset combinations is the measure built by the first and corresponding authors in their previous paper, published in PNAS in 2024, and this paper lays it down as a control. Same table, same sample, same standardisation, same authors. Measured on that footing, the effect of reusing data across subjects came out 2.4 times the effect of combining datasets unusually. That is the size of what this paper adds.

Side by side, the two tables show one more layer. In the citation model, unusualness of dataset combinations carries a coefficient of 0.1400 with p below 0.001, while repurposing does not move in that same place. The two axes touch different outcomes. Tying datasets together in unusual ways registers on both citations and disruption; carrying data across subjects registers only on disruption.

At this point the word in the title can be cashed in. Disrupting a field does not mean the research is good. It is a measurement that later work's citation flow was pulled away from the earlier literature and towards this paper. And that measurement was taken only inside a three-year window. Why the paper insists on short-term influence and nothing more comes a little later.

The earlier sections were about the side that attempted a reuse. Pulling data into a new subject, though, guarantees nothing about whether that use carries on to anyone else. It can end as one attempt by one team. The researchers measured that carrying-on separately, and the centre of gravity of this article sits here.

The diffusion measure is a single subtraction. Take the average similarity between the focal paper and the papers that used its dataset more than a year later, then subtract the average similarity with the papers that used it more than a year earlier. A positive value means later uses of that dataset shifted towards the new direction the focal paper opened; a negative value means they went back to the old ground. The theoretical range runs from −2 to 2, but the actual values cluster in a far narrower band.

3.1The shape of the distribution

The distribution tilts to one side just past zero. The median is −0.008, and the interquartile range runs from −0.023 to 0.008. 55% of the values are negative. A sign test ruled out chance as an explanation for that tilt. Among the papers that attempted a reuse, the majority saw the dataset's later users stay nearer its original application than the direction the focal paper had opened.

Reading that 55% requires the condition set out in section 1.1. It does not mean nobody used the data again. The sample is restricted to cases where some later paper did reuse the dataset, so all 12,286 papers here have downstream users. The 55% describes where those downstream users went, and in most papers they went back.

The paper offers two explanations for this low diffusion. The first is the streetlight effect. It draws on earlier work arguing that data narrows a researcher's imagination, so the direction within reach gets picked up before the more valuable but less visible one. The second is a question of sequence. Broader diffusion can only happen once the value inside the dataset's original domain has been used up, and that kind of search is hard and uncertain, so it is bound to be rare. Both are the authors' interpretations rather than mechanisms they measured.

3.2What happened when the data did cross over

Where diffusion did occur, both measures rose together. Per standard deviation of diffusion, three-year disruption was 0.0285 standard deviations higher, with p at 0.003. Three-year citations carry a coefficient of 0.0831, which converts to a rise of about 9%. Repurposing on its own could not move citations, yet once that repurposing crossed over to other people, citations moved with it.

That 9% on the citation side carries a mechanical component the paper records itself. The diffusion measure is computed from future papers that reuse the same dataset and sit semantically close to the focal paper, and those are precisely the papers most likely to cite the focal paper. Because the citation distribution is heavily skewed, even a handful of such papers can contribute meaningfully to a citation count. The authors suggest that future work drop papers in the diffusion set from the citation count, or measure citations from a period that does not overlap the diffusion window. Carrying the 9% across without that caveat turns it into an overstatement.

Attribution comes with its own condition. A positive diffusion score is an observation that later papers shifted towards the focal paper, not a claim that the focal paper caused the shift. It could be the whole field moving towards the same subject, or the value in the dataset's original domain running out. The paper records this alternative twice, once in the results section and once in the methods.

On one p-value the main text and the appendix disagree. The prose of the main text puts the relationship between diffusion and disruption at p below 0.001, but that row of appendix Table S3 shows t at 2.939 and p at 0.003. The table is the referee, so this article uses 0.003. Preprint v1 has a few more rough edges of that kind. The main text calls the appendix tables Tables 5–212, the appendix heading says there are 15 of them, and the regression tables that actually exist number 14.

The third question is about people. Which teams move data to a different place, and whose move gets taken up by others? The researchers ran ten models, entering seven team variables one at a time. The controls are only three (unusualness of dataset combinations, number of datasets, and dataset usage frequency), and the sample is the same 12,286 papers as in the previous sections.

Appendix Tables S5 to S14 of arXiv:2609.16736, merged into one table. Each coefficient comes from the individual model for that variable, and "not significant" marks the cases where the 95% confidence interval crosses zero. The diffusion coefficient for team experience is −0.0020 (Table S11), and because the same value also appears for a different variable in Table S10, any citation of it needs the table number attached.

The first thing the table shows is a row missing from the abstract. On the repurposing side the largest coefficient belongs to developed-country affiliation, at 3.1 times institutional influence. The abstract does not mention that axis. The row often read as evidence that industry is good at recycling data is not quite that either. The significant row is teams that mix academia and industry; teams made up of industry alone were not significant in either model.

The paper's own count runs like this. On the repurposing side six of the seven coefficients are significant; on the diffusion side only three are, and they are much smaller. That those three are team size, institutional influence and the academia-industry mix is where the paper brings in a disciplinary difference. Fields such as the social sciences, which draw findings out of data, require long passages back and forth between question and material, whereas innovation in AI leans more on collaboration and compute. The three surviving axes are closer to the capacity to pull in people and resources than to experience.

4.1Significant and explained are two different words

The abstract says team characteristics do a poor job of pinpointing which repurposing gets adopted, and in the very next sentence says successful adoption is more common in larger teams. Read together they look self-contradictory; look at the tables and they are not. The two sentences are describing different things.

Read from the goodness-of-fit rows of Tables S5 to S14 in arXiv:2609.16736. The ratio and the count of non-significant models are ours. On the diffusion side, the models that failed the overall F test are the ones for team experience, country status and sector background.

The gap between the two rows runs from 80-fold to more than 200-fold. Once a sample passes twelve thousand papers, a model that explains 0.001 can still produce a coefficient significant at p = 0.002. The direction is visible; the separation is barely explained. So the accurate statement is this. Team characteristics tell you something about who starts a repurposing. They tell you nothing about whether that repurposing gets taken up, at least not through team experience. Blend the two sentences and you manufacture a finding that is not there.

One layer further down, most of the explanatory power on the repurposing side does not come from teams either. The R² values of the five models sit almost on top of each other at 0.082, 0.082, 0.083, 0.094 and 0.082, and one control variable common to every model dominates with a t value of 31.6. That variable is dataset usage frequency. In the five diffusion models its sign flips, and it stays significant at around −0.012. Papers using frequently used datasets scored higher on repurposing, and yet the extent to which that repurposing travelled onward was lower. That has to be read alongside the fact that dataset popularity takes most of the explanatory power of the repurposing score. No baseline model with controls alone is reported, so the exact increment cannot be known, but judging from the differences between tables, the explanatory power the team variables add is somewhere between zero and about 1.2 percentage points. That estimate is ours.

One word needs care here. This paper has no predictive model. There is no held-out performance metric, no cross-validation, no area under a curve. The paper has observational regression and its explanatory power, and nothing beyond that. This article therefore avoids the word prediction and writes in terms of association and explained variance. Why picking out research impact in advance is hard came out along the same grain in the observation that authors ranking their own papers beat the review scores.

4.2Where the sign flips against the authors' own earlier paper

The paper writes one tension into its own main text. Earlier work held that small, less experienced teams are the ones who put data to new uses, while these results say large, experienced teams do the repurposing. That earlier work is the authors' own 2024 PNAS paper. The paper takes the reversal only on the team-size and diffusion side: small teams may be better placed to push a disruptive idea, but large teams have more capacity to help with the diffusion and adoption that follow. Nowhere in the text is there an explanation of why the sign is reversed for the act of repurposing itself.

Still, the two results are not in direct contradiction. The two papers measure different axes. The earlier paper measured the unusualness of dataset combinations; this one measures subject distance. And in this regression the earlier axis enters as a control variable. The accurate statement reaches as far as this: the two papers measure different axes, and on those two axes the sign for team size comes out opposite. There is also one difference in design. The ten team-characteristic models contain no publication-year dummies. That sets them apart from the models in the previous sections, and neither the main text nor the captions mentions the difference.

That is what the paper measured. Now for the conditions that attach to those results. The point is not to cut the paper down. The authors numbered five limitations for themselves, admitted the possibility that their instrument was contaminated, and reran the analysis with a different embedding. The job left here is to turn those self-declarations into a way of reading, and to add a few places the paper does not write down.

5.1Does the dispute over the disruption index reach this design

The disruption index is one of the noisiest quantitative measures in scholarship right now. A month ago the dispute reached the formal record. The lineage below makes clear where this paper stands.

Bibliographic details verified through PubMed and publisher records. The rebuttal and the original authors' reply appeared together in the same issue of Nature on 12 August 2026. The preprint we read still cites the 2024 arXiv version of Holst et al.; since it was submitted a month after formal publication, there may not have been time to take the final version in.

The verdict runs as follows. The main force of the criticism aimed at the disruption index is directed at the decline over time. This study claims no trend; it compares papers of the same year and the same tier side by side. It controls year as a category, controls citation counts and reference counts together, and excludes documents without references from the calculation in the first place. The data artefact identified by the August 2026 rebuttal in Nature does not reach this design.

Three things remain. First, the three-year window. The paper itself writes that its results should be read as evidence of short-term disruptive influence rather than sustained disruption. If a repurposing brought a dataset into a new subject community, early citations may arrive in a rush from that community without yet connecting to the wider lineage, and bridge-building across communities takes longer to appear. That is the authors' own account. Second, no test swapped in a different variant of the index. Third, the possibility that the repurposing measure and the disruption index are mechanically interlocked. That is the limitation the paper writes up at greatest length.

In the same place where they write that limitation, the authors also mount the counter-argument. A repurposing paper almost always cites the original source of its dataset, so later papers could just as easily have cited the source and the repurposing paper together, producing the shape of a bridge. If what actually appeared is the shape of a split, that reflects what the community built on top of the repurposed data rather than an artefact of the measurement. On top of that, the repurposing score is computed from the content of a paper before any citation exists, while the disruption index is determined by the citations that come afterwards. The association between the two measures, the authors write, is a relationship between an act of data use and the influence that follows it, not a bookkeeping artefact. The residual worry reaches only this far: controlling for reference counts and citation counts does not make the overlap disappear entirely. That admission sits in the same paragraph.

5.2Keeping fact and interpretation apart

Here the constraints the paper writes for itself are set down separately from the observations this article added while reading the tables. The first six are the paper's own statements. The last four are things we found by checking the tables against each other, and they are not written anywhere in the paper.

• [The paper's own statement] These are observational associations. The authors open their policy suggestions with the conditional "if this association reflects a causal effect", and recommend further experiments or causal work.
• [The paper's own statement] Papers with Code, the source, has unclear inclusion criteria and concentrates on mainstream venues, which limits how representative it is.
• [The paper's own statement] More than 20,000 papers were dropped because their metadata could not be matched, which may have introduced selection bias by country, institution and venue.
• [The paper's own statement] The results are short-term effects inside a three-year window. Separating temporary from lasting effects needs longer follow-up work.
• [The paper's own statement] The possibility of mechanical overlap between the disruption index and the repurposing measure remains.
• [The paper's own statement] The association between diffusion and citations may carry a mechanical component too.
• [Our observation] Papers whose dataset was never reused afterwards are excluded from the sample. That condition is missing from the paper's list of limitations, and it is needed to read the diffusion distribution.
• [Our observation] The ten team-characteristic models have no publication-year dummies. The design differs from the models in earlier sections, and the paper does not mention it.
• [Our observation] There are only two robustness checks. The one that redrew three figures with an alternative embedding produced figures alone, so it can say no more than that the direction held; the one that reran the analysis including arXiv preprints has neither table nor figure, only a single sentence saying the results were similar. There is no check that varied the citation window, none that swapped in a different variant of the index, and none that corrected for sample selection bias. Every standard error was computed without a robustness correction.
• [Our observation] The same result is written slightly differently in the abstract, the Significance Statement and the main text, and on the p value for diffusion and disruption the main prose and the appendix table disagree.

The paper states that code and data will be released on publication, and as of 17 September 2026 the repository is empty. That matches what was promised, so it breaks nothing. It does mean that at this moment there is no asset with which anyone outside can rerun these results, and since leaving things in a reusable state is the subject of this article, the fact is worth recording.

5.3Distance from an earlier study of the same platform

One other study looked at the same platform at almost the same time: the analysis of dataset lifecycles that Koch and three co-authors presented at NeurIPS 2021. Covering 2015 to 2020, it found three things. Concentration on a few datasets was intensifying inside task communities; datasets borrowed from other tasks were being adopted at a substantial rate; and usage was skewed towards datasets created by a small set of elite institutions. In numbers, the per-task Gini coefficient had a median of 0.60 in 2020, and the share of datasets borrowed from a different task had a median of 57.8%. That borrowing rate split sharply by field, reaching 71.9% in computer vision while natural language processing stopped at 27.4%. And as of June 2021, 12 institutions accounted for more than half of all dataset usage.

All three findings interlock with this paper. The second is the very phenomenon this paper quantified, the third points the same way as its institutional-influence coefficient, and the first is a different measurement of the same phenomenon as the negative median diffusion. Yet this paper cites Koch et al. only as a precedent for the data source and never responds to their findings. That is context worth knowing rather than a defect. Of the two, Koch et al. measured the distribution and this paper measured outcomes. What becomes visible when the same data is used over and over in several places came up in our audit of redundancy in physical AI benchmarks.

A gap in time needs stating here. The corpus read so far is a 2021 snapshot, while the events discussed below fall between 2024 and 2026. Nothing here suggests the paper foresaw the present moment. An academic bridge is nonetheless already in place. The Epoch AI researchers who estimated when the stock of public human-written text runs out listed three ways out, and one of them is transfer from data-rich domains. Pulling data from somewhere else into this work is exactly what this paper measured.

Reusing anything, however, starts with being able to find it. How that layer can disappear is demonstrated by this paper's own source.

6.1The platform that produced the sample is already gone

Those 12,286 papers came out of the June 2021 snapshot of Papers with Code. That platform shut down around 24 July 2025. The closure was confirmed when a Hugging Face co-founder announced the next day that they would build a successor service together, and the final public snapshot, collected on 28 and 29 July 2025, survives in a preservation organisation on Hugging Face under CC BY-SA 4.0. Every dataset card there carries a warning that it will no longer be updated.

The size at closure has to be corrected first. Several second-hand reports cite a figure of 18,000 papers as though it were the platform's size when it closed, but that number comes from the December 2019 announcement of the Facebook acquisition. Counting the final snapshot directly gives 576,261 papers, 15,008 datasets and 300,161 links between papers and code. It grew 32-fold in about five and a half years, so using the old figure as the closing size understates the reality by a factor of 32.

The state of things after the shutdown carries the more concrete lesson. The main document of the original repository still says the data is regenerated daily. A pull request opened on 10 September 2025 to fix that line and record the snapshot collection date has still not been merged. An issue asking whether the project had really closed went up in August 2025 and remains open without an answer. The successor service never inherited the per-task leaderboards that were central to the old platform. Survival of the data now rests on voluntary preservation by assorted individuals and organisations rather than on one company keeping the lights on.

A contrasting design exists in the same period. Croissant, released by MLCommons on 6 March 2024, is not one company's specification but a metadata standard from a consortium mixing academia, industry and government bodies. Kaggle, Hugging Face and OpenML all announced support at launch, and the February 2026 version added provenance tracking and governance tags. Adoption is not merely formal either. In the NeurIPS 2025 datasets and benchmarks track, 426 of 497 accepted papers, or 85.7%, attached a retrievable Croissant document. Our piece on standardising the conditions for reusing robot data and our survey of the standards landscape in South Korea each looked at this layer from a different angle. Adopting a format is one measure, and actually filling in its required fields is another.

6.2Documentation follows popularity

One study counted, across the whole population, how much of a dataset card actually gets filled in. Analysing 7,433 cards on the Hugging Face Hub, it found that 86.0% of the 100 most-downloaded datasets completed all five recommended sections, against 7.9% of datasets with zero downloads. The section that holds licensing and cautions accounted for 2.1% of all card text. Documentation piles up on data that is already well used, and the less discovered a dataset is, the fewer clues exist for discovering it. Our piece on the research data pipeline sets out separately what it takes for stored data to actually get used.

Broken down by language, Korean is the thinnest. The figures come from a study comparing the top 700 datasets per language on the Hugging Face Hub.

Taken from the CJK dataset comparison by Choi, Park and Song (arXiv:2507.04329). The sample is the top 700 datasets per language with at least 100 downloads, not the hub as a whole. The share of unknown licences for Japanese is absent from the original and is left blank here.

Korean has the highest share of unknown licences and the lowest scores for documentation completeness and academic linkage. Seen from the position of someone trying to reuse the data, the three rows say the same thing. Korean data, even once found, comes with too little on which to judge whether it can be used.

Without a record, even the fact that data was used leaves no trace. A 2026 study queried citations to the 64,774 datasets in the open repository Dryad through three separate sources, and the counts came out at 46,873, 54,335 and 492. No single source covered everything, so the researchers combined all three. The source that found the fewest is the one that looks at the scholarly citation network. An analysis of medical imaging conference papers found that 21.6% used open data while recording it only in a footnote or a URL rather than a formal citation, and in another 5.0% there was no citable object at all. As section 1 showed, this is also why the paper counted repurposing from platform usage records instead of from citations.

6.3In South Korea the same problem surfaced as duplicate construction

An audit of AI training data by the Board of Audit and Inspection of Korea, released on 12 August 2026, put a measured cost on this. Between 2017 and 2024, the budget spent building public AI training data came to KRW 1.63 trillion (about $1.1 billion), and 908 datasets were published on AI Hub, the national open data portal. The problem sits next to that figure. Twenty-six public institutions had posted 313 datasets only on their own portals, where nobody could search for them. What cannot be found cannot be reused, and what cannot be reused gets built again. Among the cases the audit confirmed, 5,200 of 9,000 household waste images built by Seo-gu district in Daejeon, or 57.8%, resembled a 2020 build by the Ministry of Science and ICT, and in wildlife data from the Korea Expressway Corporation, 25,000 of 60,000 images, roughly 42%, resembled a 2021 build. We covered that audit in detail last month.

The Korean picture supplies one answer to why the paper's diffusion distribution leans negative. In the paper's sample the data went back to the subject it had originally served; in the Korean cases it was never in a position to cross anywhere. Absent from the catalogue, a repurposing is never even attempted.

A case pointing the other way arrived in the same month. On 27 August 2026 the Ministry of Science and ICT and the National Information Society Agency opened 29 datasets, some 35.44 million items and 1.56 trillion tokens, built by the companies taking part in the sovereign AI foundation model programme, for anyone to download from AI Hub. They were produced on a 2025 data construction and processing budget of KRW 15 billion (about $10 million), and data requiring security clearance is routed through a secure enclave. Painting South Korea purely as a failure case sees only half of it. On one side is a record of things rebuilt because they could not be found; on the other, a record of things released so they can be used again.

Pressure that thins the layer itself arrives alongside. On 1 July 2025 Cloudflare introduced an opt-in setting to block AI bots on pages monetised through advertising, and in the same announcement published crawl-to-referral ratios. As of June 2025, Google crawled 14 times per referral, OpenAI 1,700 times and Anthropic 73,000 times. The other face of a drying commons is something we examined on the Wikipedia side, and the concentration of data supply in few hands we set out separately.

The bridge from this paper to practice is the diffusion distribution set out earlier. When the hit rate is low, value has to come from the number of attempts you can afford. At the level of an organisation, then, the task is not to pick which dataset will strike gold but to lower the cost of one attempt. From here on this is our inference. The paper never says to invest in documentation. The authors' closing paragraph offers a hypothesis rather than a result: the return may be unusually large once the four barriers named earlier come down. They left the test to later work.

Against an organisation's own datasets, that hypothesis turns into four things to check. The last column of the table below records what gets blocked when the item is missing.

These four items translate the three of the paper's four candidate interventions that concern the data itself (discovery, documentation and interoperability) into a checklist at the level of an organisation. The composition of the items and the final column are our interpretation, and no such table exists in the paper. The example in the third row comes from the audit by the Board of Audit and Inspection, and the figure in the second row from the CJK comparison in section 6.2.

Of the four, the third breaks most often in practice. Data goes unused because nobody knows it exists more often than because its quality is poor. The second comes back as cost. Using data whose licensing was never sorted out adds a bill for checking after the fact, and how large that bill gets is something we worked through in our piece on the cost of auditing open dataset licences.

The paper's own policy suggestions point the same way. The authors propose that data repositories surface papers from distant research areas that reused similar datasets, that conference submission systems flag datasets used only within a narrow subject, that language-model-based recommendation suggest pairings of dataset and subject not yet attempted, and that curation practices and repositories publish a summary of which subjects a dataset has been used for so far. That last item amounts to recording usage history as metadata. It is also a field absent from most data cards today.

A large part of what Pebblous sells is the work of putting data into a state where it can be used again. DataClinic diagnoses an existing dataset and reports what is missing, and AI-Ready data work records the purpose, conditions and limits of collection so that the next person can use the data. This paper offers a large-scale measurement of how the thing that work aims at, data moving from its original place to another one, related to research outcomes.

8.1The business and technology link

Until now the axes for valuing a dataset have mostly been size and accuracy. The axis this paper adds is the capacity to move somewhere else, and it speaks about that capacity in terms of outcomes. Three of the four candidate interventions in the paper's closing paragraph overlap with our own list of work: dataset discovery, documentation and interoperability. The fourth, cross-domain training in data use, is a task for an organisation's education rather than for tooling. The paper did not verify those four. It put them forward as hypotheses, and this link holds only as long as that distinction does.

8.2The data quality angle

What this paper measures is not the internal quality of data but the distance it travels in subject space. Internal measures such as accuracy or completeness do not capture whether data can be moved to another purpose. A dataset with no missing values and perfect labels still tells the next person nothing about how far it sits from their own question, if the collection conditions, the measurement environment, the label definitions and the exclusion criteria were never recorded. Pointing out which items in a quality characteristics standard bear on reusability connects this to the existing discussion, and that connection is a bridge we are building rather than anything in the paper.

The language table in section 6.2 shows why this axis is a more expensive problem in South Korea. Korean datasets sit among the lower scores for documentation completeness and carry the highest share of unknown licences. A good quality diagnosis still leaves that data unable to cross to the next person.

8.3What this means for customers and partners

Three things carry over from this paper's distribution into practice.

• Is there a procedure for counting what you already hold before collecting anything new? This is a question of how budget is split between building data and reusing it. The audit in section 6.3 shows what happens in the Korean public sector when that procedure is missing.
• What blocks reuse is usually not quality but the absence of a record. Licence terms, the scope of consent at collection, exclusion criteria. With those three fields empty, second use stops regardless of the quality score.
• A single attempt has a low chance of paying off, so the cost of attempting has to come down. That is our inference from the observation that the diffusion distribution leans negative, not a claim the paper makes. The instruments for lowering that cost are documentation and catalogues.

8.4Where Pebblous stands

Here is the ground for taking a step from data quality diagnosis towards assessing reusability. The shutdown in section 6.1 widens what such an assessment has to cover. The value of reuse rests not only on properties of the data itself but on the layer that makes the data findable, and that layer can vanish through a single operating decision at a single company. That is why diagnosis and documentation have to live inside the organisation. When the layer outside closes, what is left is only what the organisation wrote down for itself.

The figures in this article come from three streams. Values from preprint 1 were transferred by checking the public arXiv version's main text and its 14 appendix regression tables directly, and no value was read off a figure by eye. Industry facts were retrieved from platform APIs and official announcements. Korean audit figures were carried over only where two or more outlets reported the same value, and we could not open the audit report itself.

The backbone of this report

• 1.Yulin Yu, Yong-Yeol Ahn, Daniel M. Romero. "Dataset repurposing and disruptive AI research." Preprint, arXiv:2609.16736v1 [cs.CY], submitted 15 September 2026. arXiv: 2609.16736 — the primary source for this article. The authors are affiliated with the College of Information Science at the University of Arizona, the School of Data Science at the University of Virginia and the School of Information at the University of Michigan, and the work was supported by US National Science Foundation grant 2404109. The arXiv Comments field is empty, so we read it as an unrefereed preprint. Code and data are listed as forthcoming on publication. Section 5.2 records where that stands now.
• 2.Yulin Yu, Daniel M. Romero. "Does the use of unusual combinations of datasets contribute to greater scientific impact?" PNAS 121(41):e2402802121, 2024. DOI 10.1073/pnas.2402802121 — the scale used in section 2.2 and the counterpart whose sign flips in section 4.2. This paper lays that study's measure down as a control and measures a new axis on top of it. Publisher access was blocked, so the full text could not be opened, and we carried over only what paper 1 cites from it.

Prior work and measurement tools

• 3.Bernard Koch, Emily Denton, Alex Hanna, Jacob G. Foster. "Reduced, Reused and Recycled: The Life of a Dataset in Machine Learning Research." NeurIPS 2021 Datasets & Benchmarks. arXiv:2112.01716 — section 5.3. It looked at the same platform over almost the same period and measured the distribution. Paper 1 draws on it only to justify its choice of source. The Gini coefficient of 0.60, the median adoption rate of 57.8% and the 12-institution figure in section 5.3 were checked directly against the PDF of this paper. The 12 institutions come from the main table for the June 2021 snapshot, which is a different table from the 9-institution one in the robustness appendix.
• 4.Amanpreet Singh, Mike D'Arcy, Arman Cohan, Doug Downey, Sergey Feldman. "SciRepEval: A multi-format benchmark for scientific document representations." EMNLP 2023, 5548–5566 — cited by paper 1 as the source of the SPECTER2 embedding used by the repurposing measure in section 1.2.
• 5.Zihang Lin, Yian Yin, Lu Liu, Dashun Wang. "SciSciNet: A large-scale open data lake for the science of science research." Scientific Data 10(1):315, 2023 — the source of the bibliographic records and citation network in section 1.1. Its citation counts stop at 2022, so three-year citations were supplemented from the August 2024 OpenAlex snapshot.
• 6.Brian Uzzi, Satyam Mukherjee, Michael Stringer, Ben Jones. "Atypical combinations and scientific impact." Science 342(6157):468–472, 2013 · Margaret A. Boden. "Creativity and artificial intelligence." Artificial Intelligence 103(1–2):347–356, 1998 — the original sources of the two theoretical frames paper 1 invokes. For Boden, the cited version is the 1998 journal article rather than the book.
• 7.Johannes Hoelzemann, Gustavo Manso, Abhishek Nagaraj, Matteo Tranchero. "The streetlight effect in data-driven exploration." NBER Working Paper 32401, 2024 · Ryan Hill et al. "The pivot penalty in research." Nature 642(8069):999–1006, 2025 — the works paper 1 puts forward as candidate explanations in sections 3.1 and 2.1. The second one it raised and then withdrew itself.

The disruption index and the dispute around it

• 8.Russell J. Funk, Jason Owen-Smith. "A dynamic network measure of technological change." Management Science 63(3):791–817, 2017 — the origin of the index unpacked in section 2.
• 9.Michael Park, Erin Leahey, Russell J. Funk. "Papers and patents are becoming less disruptive over time." Nature 613(7942):138–144, 2023. DOI 10.1038/s41586-022-05543-x — the paper that started the dispute.
• 10.Vincent Holst, Andres Algaba, Floriano Tori, Sylvia Wenmackers, Vincent Ginis. "Dataset artefacts can partially drive the measured decline in disruption." Nature 656(8127):E7–E13, 12 August 2026. DOI 10.1038/s41586-026-10787-y · Michael Park, Erin Leahey, Russell J. Funk. "Reply to: Dataset artefacts can partially drive the measured decline in disruption." Nature 656(8127):E14–E21, 2026. DOI 10.1038/s41586-026-10788-x — the two rows in the table in section 5.1. Bibliographic details were verified through PubMed, and since the full texts could not be opened, no quantitative figures were carried over. Paper 1 cites the first of these in its 2024 arXiv preprint version.
• 11.Alexander M. Petersen, Felber Arroyave, Fabio Pammolli. "The disruption index is biased by citation inflation." Quantitative Science Studies 5(4):936–953, 2024 · Christoph Leibel, Lutz Bornmann. "What do we know about the disruption index in scientometrics?" Scientometrics 129(1):601–639, 2024 — the basis for criticism ① in section 5.1 and for the discussion of window sensitivity.
• 12.Lingfei Wu, Dashun Wang, James A. Evans. "Large teams develop and small teams disrupt science and technology." Nature 566(7744):378–382, 2019 — the prior work paper 1 sets against its own result in section 4.2.

Data reuse infrastructure and documentation

• 13.The pwc-archive organisation on Hugging Face — the final public snapshot of Papers with Code (collected 28–29 July 2025, CC BY-SA 4.0). The closing size given in section 6.1, 576,261 papers, 15,008 datasets and 300,161 links, was counted directly from this organisation's dataset cards and API responses. Its cards are flagged as frozen.
• 14.Robert Stojnic. "Papers with Code is joining Facebook AI." Medium, 13 December 2019 — the figures in this post, including the 18,000 papers, are values as of the 2019 acquisition. Several second-hand reports cite them as the platform's size at closure, which section 6.1 corrects.
• 15.MLCommons. Release of the Croissant metadata specification (6 March 2024) and Croissant 1.1 (February 2026), plus the NeurIPS 2025 Datasets & Benchmarks adoption count (426 of 497 accepted papers) — section 6.1. Checked against the official MLCommons announcement and the Google Research blog.
• 16.Xin Yang et al. "Navigating Dataset Documentations in AI: A Large-Scale Analysis of Dataset Cards on Hugging Face." ICLR 2024. arXiv:2401.13822 — the source of 86.0%, 7.9% and 2.1% in section 6.2. It analyses all 7,433 cards in its population, not the entire hub. The citation-tracking figures in the last paragraph of the same section come from two separate studies. The counts from querying 64,774 Dryad datasets through three sources (46,873 / 54,335 / 492) are the authors' own queries in "Sustaining Dryad" (arXiv:2604.27580), run in February and July 2025. The 21.6% recorded without a formal citation and the 5.0% with no citable object come from Heller et al.'s analysis of MICCAI papers from 2014 to 2018 (arXiv:1908.06830). This report checked both values directly against the original PDFs.
• 17.Yebin Choi, Jaehyung Park, Hyunsoo Song. "No Language Data Left Behind: A Cross-Cultural Study of CJK Language Datasets in the Hugging Face Ecosystem." arXiv:2507.04329 — the per-language table in section 6.2. The sample is the top 700 datasets per language. The author attribution needs rechecking.
• 18.Timnit Gebru et al. "Datasheets for datasets." CACM 64(12):86–92, 2021 — the origin of the documentation specification, and a work that appears in paper 1's own reference list.
• 19.Pablo Villalobos et al. "Will we run out of data? Limits of LLM scaling based on human-generated data." arXiv:2211.04325 (v2, 4 June 2024) — the three ways out mentioned at the start of section 6. Paper 1 does not cite this study. The bridge is ours.
• 20.Cloudflare. "Control content use for AI training." Official blog, 1 July 2025 — the last paragraph of section 6.3. The original describes an opt-in setting limited to pages monetised through advertising; second-hand reports describing it as blocking by default widen that scope. The crawl-to-referral ratios are also first-hand figures from this post.

Korean sources

• 21.Board of Audit and Inspection of Korea. Audit findings, "The State of AI Industry Promotion III (AI Training Data)", released 12 August 2026 — the source of KRW 1.63 trillion, 908 datasets, 313 datasets, Seo-gu Daejeon at 57.8% and the Korea Expressway Corporation at about 42% in section 6.3. The original audit report was not consulted, and only figures corroborated by at least two news outlets appear here. The values of 63% and 58% circulating in search engine summaries are absent from the underlying articles and were not used.
• 22.Ministry of Science and ICT and National Information Society Agency. Announcement of the data release from the sovereign AI foundation model programme, 27 August 2026 — the source of the 29 datasets, 35.44 million items, 1.56 trillion tokens and KRW 15 billion in section 6.3. Cross-checked across multiple outlets reporting the ministry announcement.

Related posts on the Pebblous blog

• 23.The audit of duplicate construction in Korean public AI training data — the basis for section 6.3. It covers in detail the record of things rebuilt because they could not be found.
• 24.A drying commons and concentration in data supply — referenced respectively in the last paragraph of section 6.3.
• 25.What stored research data goes through before it is used and the cost of auditing open dataset licences — referenced in sections 6.2 and 7 respectively.
• 26.Standardising the conditions for reusing robot data, the AI-Ready data standards landscape in South Korea, the audit of redundancy in physical AI benchmarks and author rankings against review scores — each referenced in a single line in sections 6.1, 5.3 and 4.1.