This Guest Post identifies falsified results, theoretical, methodological, and analytical problems in the paper "Learning to innovate: How and when firms transform intellectual capital into exploratory and exploitative innovation" appeared in the Strategic Entrepreneurship Journal (SEJ) Volume 20, Issue 3. The editor(s) and reviewers completely failed to detect the data and results fabrication and other highlighted stern issues. The SEJ is indexed/abstracted in FT50, Clarivate’s SSCI (Impact Factor for 2025: 6.7), Scopus (Q1), ProQuest, Inspec etc. SEJ charges a hefty open access fee of USD 4,510. The glimpse of the findings is tabulated in Table R1 below:

Findings at a Glance

Table R1: Principal findings and their implications

Finding	Evidence	Consequence
F01–F03	Impossible adjusted R² ordering and unreconciled OLS fit statistics	The printed model results cannot all describe the stated analyses.
F04–F06	Conflicting mediation equations, 56/60 repeated control coefficients, reverse-test asymmetry	Original outputs and table provenance are essential.
F07–F08	Indirect-path products, conditional-effect changes, and interaction signs conflict	Mediation and moderated mediation estimates need complete reproduction.
F09–F12	Significance, measurement statistics, CFA fit, and descriptive reporting issues	Validity and inferential summaries require recalculation and clarification.
F13–F21	Temporal, source, sampling, and construct limitations	Causal and replication claims exceed the observed design.
F22–F30	Incomplete interaction models, robustness evidence, and theoretical overreach	Revised models and narrower conclusions are required.

Numerical Coherence of The Results

F01: Adjusted R-Sq exceeds R-Sq in nine models

Critical; established inconsistency. Location: Table 3, p. 16, and Table 6, p. 23.

Table 3 reports adjusted R-Sq greater than R-Sq in Models 2, 3, 4, 7, 9, 10, 11, and 12. Table 6 repeats the problem in Model 3. For a conventional model with an intercept, n observations, and p predictors, adjusted R-Sq equals 1 − (1 − R-Sq)(n − 1)/(n − p − 1). When p is positive and R-Sq is below one, adjustment reduces R-Sq. Ordinary rounding cannot reverse that ordering.

Table R2: Published adjusted R-Sq values greater than R-Sq

Model	R-Sq	Adjusted R-Sq
Table 3 M2	.23	.24
Table 3 M3	.15	.16
Table 3 M4	.21	.22
Table 3 M7	.36	.37
Table 3 M9	.27	.28
Table 3 M10	.23	.24
Table 3 M11	.26	.28
Table 3 M12	.35	.36
Table 6 M3	.15	.16

The problem is broader than one transposed cell. For example, Table 3 Model 2 has n = 296, nine predictors, and R-Sq = .23. The standard adjustment gives approximately .206, which rounds to .21, rather than the reported .24. The same formula should be applied to every model using its actual analysis sample and predictor count. A correction must regenerate both rows from software output and check whether model labels, sample sizes, or entire columns have been displaced.

F02: Several R-Sq values violate a lower bound imposed by included predictors

Critical; conditional mathematical inconsistency. Location: Table 2, p. 14; Table 3, p. 16; Table 4, p. 17.

In an ordinary least-squares regression with an intercept, adding predictors cannot reduce in-sample R-Sq. Consequently, the full model’s R-Sq must be at least the square of the correlation between its outcome and any included predictor, when the correlation and regression use the same observations and variables. Several reported models fail this basic check.

Table R4: Minimum R-Sq required by a reported included predictor

Model and outcome	Included predictor	r	r²	Reported R²
Table 3 M1 CLT	Exploration at T1	.40	.1600	.05
Table 3 M3 exploration	Exploration at T1	.49	.2401	.15
Table 3 M4 exploration	Exploration at T1	.49	.2401	.21
Table 3 M8 exploitation	Exploitation at T1	.50	.2500	.11
Table 3 M10 exploitation	Exploitation at T1	.50	.2500	.23
Table 4 exploitation	Exploitation at T1	.50	.2500	.19

The lower bound assumes the same observations, variables, and conventional OLS specification. These discrepancies survive two-decimal rounding. For example, a correlation reported as .49 is at least approximately .485, whose square is .2352. It cannot coexist with a full-model R-Sq reported as .15 or .21. Different samples, weighting, transformations, or nonstandard definitions could break the comparison, but those differences are not disclosed in the reported OLS analyses. The remedy is to identify the exact sample and variable definitions behind each table and reproduce the correlation and regression outputs together.

F03: The correlation matrix does not reproduce the stated regressions

Critical; conditional mathematical inconsistency. Location: Tables 2 and 3, pp. 14 and 16.

For standardized OLS using the same complete cases, the coefficient vector is determined by the predictor correlation matrix and the predictor–outcome correlations. Solving those equations for the ten models in Table 3 that do not contain product terms yields the following values. Models 7 and 12 cannot be reconstructed because correlations involving their interaction terms are not reported.

Table R5: Study 1 R² reconstructed from Table 2

Model	Outcome and predictors	Reported R²	Reconstructed R²
M1	CLT; controls	.05	0.2669
M2	CLT; controls + IC	.23	0.3218
M3	Exploration; controls + IC	.15	0.3298
M4	Exploration; controls + IC + CLT	.21	0.3488
M5	Exploration; controls + breadth	.25	0.3099
M6	Exploration; controls + depth	.26	0.2931
M8	Exploitation; controls + IC	.11	0.3333
M9	Exploitation; controls + IC + CLT	.27	0.3463
M10	Exploitation; controls + breadth	.23	0.3077
M11	Exploitation; controls + depth	.26	0.3222

Controls are the eight controls displayed in Table 3. These reconstructions are conditional consistency checks, not raw-data reanalyses.

The mismatch concerns substantive coefficients as well as fit. Model 2’s standardized IC coefficient reconstructs to approximately .271, compared with .37 in Table 3. Model 4’s CLT coefficient reconstructs to approximately .167, compared with .33. Model 9’s CLT coefficient reconstructs to approximately .139, compared with .26. Neither correlation matrix has a negative eigenvalue, so this is not a claim that the matrices themselves are mathematically impossible.

A diagnostic sensitivity calculation perturbed each Study 1 off-diagonal correlation within ±.005 in 10,000 draws. Model 2’s IC coefficient ranged from approximately .258 to .283 and its R² from .313 to .332. This simulation is not an exhaustive proof over every rounding combination, but it shows that ordinary rounding offers no persuasive explanation for the large discrepancy. The lower-bound checks in F02 provide the stronger deterministic evidence. Original correlation, scoring, missing-data, and regression files are necessary to identify which published quantities belong together.

F04: The two presentations of the mediation outcome equations disagree

Critical; established reporting conflict, conditional on identical specifications. Location: Table 3 Models 4 and 9, p. 16; Table 4, p. 17; mediation discussion, p. 15.

Table 4 lists the same eight controls, IC, and CLT that appear in the corresponding mediation outcome equations in Table 3. Yet the point estimates and R-Sq values differ. For exploratory innovation, IC changes from .22 to .17, CLT from .33 to .31, firm size from −.08 to +.12, and R-Sq from .21 to .26. For exploitative innovation, IC changes from .19 to .15, CLT from .26 to .24, firm size from −.13 to +.14, and R-Sq from .27 to .19.

OLS and the OLS outcome equation in PROCESS should have the same point estimates when fitted to the same data and predictors. Bootstrapping changes uncertainty estimation, not the original-sample least-squares solution. A standardized versus unstandardized distinction could change magnitudes, but cannot by itself reverse the sign of the same firm-size coefficient or change R-Sq. If the models used different samples, transformations, controls, or estimation options, these must be identified explicitly. Otherwise, the tables require correction.

F05: Control coefficients repeat extensively across independent studies

Critical reporting anomaly; origin undetermined. Location: Table 3, p. 16, and Table 6, p. 23.

Comparing the first ten displayed model columns across the two tables, 56 of the 60 coefficients in the six shared control rows are identical to two decimal places, including their signs. The rows are firm age, firm size, public/private sector, technological diversification, R&D intensity, and organizational slack. All ten firm-age coefficients and all ten firm-size coefficients repeat exactly. Each of the other four rows repeats in nine of ten positions.

For illustration, the firm-size sequence in both tables is −.06, −.03, .14, −.08, −.08, −.07, −.05, .09, −.13, −.09. This comparison deliberately follows the printed column order. The columns do not always represent equivalent models. That makes the repetition especially relevant to a possible table-construction problem, rather than demonstrating replication of the same effects.

The studies have different samples, industries, sample sizes, innovation measures, control structures, and estimators. Extensive repeated sequences therefore require reconciliation with independent original outputs. No probability of accidental duplication is assigned here because such a probability would require assumptions about dependence and rounding. The pattern is consistent with a possible copy or carryover error; it does not establish how the table was produced or whether the underlying data are genuine.

F06: The reverse-direction regression argument is not statistically coherent as described

Critical; conditional mathematical inconsistency and invalid causal inference. Location: Appendix C, empirical assessment of reverse causality; Table 3 Model 2, p. 16.

Appendix C reports IC → CLT as β = .37, p < .001, but CLT → IC as β = .08, p = .24, while stating that all controls were held constant. Under ordinary OLS on the same cases with the same controls and conventional standard errors, these two tests are tests of the same partial correlation. Their coefficients may differ, but their t-statistics in absolute value and their two-sided p-values must agree. A significant forward test and nonsignificant reverse test cannot arise merely by exchanging the dependent and focal independent variables.

Residualizing IC and CLT on the eight controls in Table 2 yields reconstructed standardized slopes of approximately .271 and .277, with the same p-value of approximately .0000024 in both directions. These are reconstructed checks, not recovered raw-data results. The exact symmetry principle does not depend on the rounding of the published correlations. Different samples, control sets, transformations, or robust variance estimators would require a different comparison and must be disclosed.

The supplementary SEM coefficients, .36 versus .06, are also uninterpretable without the full competing models, identification restrictions, fit statistics, and output. More fundamentally, a nonsignificant reverse model does not establish causal direction, and a forward indirect association need not disappear when feedback or reverse causation exists. The assertion that the reported pattern provides robust empirical support for unidirectional causality should be withdrawn unless a defensible identification design is supplied.

F07: Reported indirect effects do not reconcile with the identified component paths

Critical; conditional numerical inconsistency. Location p. 15, 20–21; Tables 3, 4, and 6; Appendix C.

In a single linear mediation model with consistently scaled coefficients, the indirect point estimate is the product of the IC → CLT path and the CLT → outcome path. Study 2 identifies these paths as .39, .37 for exploration, and .34 for exploitation, but reports indirect effects of .11 and .09. The products are .1443 and .1326. Allowing all component paths to vary within their two-decimal rounding intervals gives product ranges of approximately .1405–.1481 and .1290–.1363. These cannot round to .11 and .09, respectively.

Study 1 is also unreconciled. Combining its .37 IC → CLT path with Table 4’s .31 and .24 outcome paths give .1147 and .0888, while Table 4 reports .13 and .11. Appendix C additionally reports the exploitative indirect effect as .10, whereas the main mediation presentation gives .11. Mixing standardized and unstandardized estimates, or paths from different PLS score solutions, can make an informal product comparison invalid. That possibility is precisely why the paper must identify the complete model and scale behind each estimate. As printed, the reader cannot assemble a consistent path system supporting the claimed indirect effects.

F08: Conditional indirect effect changes and interaction signs conflict

Critical; established arithmetic and reporting inconsistencies. Location: p. 21 and 24; Table 6, p. 23.

For knowledge breadth, Study 2 reports conditional indirect effects of .19, .23, and .26 at low, mean, and high moderator levels. The text says that the mean-to-high increase equals .072. The printed increase is .26 − .23 = .03. Even after rounding, that difference lies approximately between .02 and .04, not .072. The low-to-high difference is .07, which suggests a possible mislabelled contrast, but that explanation must be checked against output.

For knowledge depth, the corresponding effects are .17, .21, and .25. The mean-to-high increase is .04, with an approximate rounding interval of .03–.05, rather than the stated .065. The text also describes the cross-interactions as positive, ω = .021 for depth predicting exploration and ω = .018 for breadth predicting exploitation. Table 6 gives negative interaction coefficients, −.05 and −.03, respectively.

The quantities labeled ω, Δ, interaction coefficient, and conditional indirect effect are not adequately distinguished. A path interaction, an index of moderated mediation, and a one-standard-deviation contrast are different quantities. If ω belongs to another model, that model must be reported. The mean-level conditional indirect effects of .23 and .21 also need reconciliation with the earlier unconditional indirect effects of .11 and .09. Different model specifications could explain that last comparison, but no explanation is provided. All these quantities should be regenerated from one clearly documented set of equations.

F09: Some correlation significance symbols cannot follow from the stated sample sizes

Major; conditional inconsistency. Location: Table 2, p. 14, and Table 5, p. 22.

For a conventional two-sided Pearson test, r = .10 with n = 296 gives p ≈ .086. Even the upper end of a two-decimal rounding interval, r ≈ .105, gives p ≈ .071. Thus, a correlation displayed as .10* in Table 2 cannot satisfy p < .05 under that test and sample size. For example, the firm-size–technological-diversification cell is marked .10*. With n = 262, r = .10 gives p ≈ .106, and r = .11 gives p ≈ .076. Both remain above .05 throughout their ordinary rounding intervals. Table 5 includes these small starred coefficients, including the .10* age–sector correlation.

The paper needs to state whether its stars use one-sided tests, another correlation statistic, another sample size, or another procedure. Some values can be explained by one-sided tests, so the test convention matters. An overly coarse symbol, such as one star on a value that also satisfies p < .01, is not itself a logical contradiction because p < .01 also implies p < .05. Likewise, some .11 or .12 values can cross a threshold within rounding intervals. The concern here is limited to cells that cannot meet the usual two-sided threshold as printed.

F10: Validity and reliability statistics do not match the reported loadings

Major; conditional numerical inconsistency. Location: Appendix A, measurement items; validity discussion, p. 13 and 20.

For standardized reflective loadings and the usual simple measurement model, AVE is the mean of the squared loadings. Conventional composite reliability is the squared sum of loadings divided by that squared sum plus the sum of indicator error variances, with each standardized error variance equal to one minus its squared loading. Recalculation gives the following results.

Table R5: Measurement statistics from the listed factor loadings

Study	Construct	AVE reported	AVE calculated	CR reported	CR calculated
1	Human capital	.51	0.510	.79	0.838
1	Social capital	.55	0.580	.84	0.873
1	Organizational capital	.56	0.626	.82	0.870
1	CLT	.54	0.589	.84	0.909
1	Knowledge breadth	.62	0.662	.88	0.854
1	Knowledge depth	.64	0.668	.86	0.858
2	Human capital	.53	0.532	.81	0.850
2	Social capital	.52	0.582	.82	0.874
2	Organizational capital	.54	0.633	.83	0.873
2	CLT	.52	0.600	.82	0.913
2	Knowledge breadth	.62	0.662	.85	0.854
2	Knowledge depth	.59	0.651	.83	0.848
2	Exploratory innovation	.63	0.629	.82	0.871
2	Exploitative innovation	.60	0.584	.78	0.808

Calculated values use the conventional standardized reflective formulas described in F10. Incompatibility counts account for rounding; a visually different third decimal alone is not classified as an error.

Eleven of the fourteen AVE entries and twelve of the fourteen conventional composite reliability entries cannot be reconciled by allowing both the loadings and reported statistics their ordinary two-decimal rounding intervals. For example, Study 2 CLT has loadings .69, .79, .73, .75, .82, .78, and .85. These imply AVE ≈ .600 and conventional CR ≈ .913, compared with .52 and .82 in the appendix.

Alternative reliability estimators, correlated residuals, different loadings, or different measurement solutions would need explicit documentation. The article’s Study 2 discussion specifically refers to standardized loadings. Importantly, the recalculated figures generally still exceed conventional .50 and .70 benchmarks. The audit therefore identifies inconsistent reporting; it does not infer that every scale fails convergent validity or reliability. Corrected indicator output, error specifications, definitions of reliability statistics, and complete construct-level validity tables are required.

F11: The CFA fit statistics require reconciliation and fuller model identification

Major; conditional numerical and specification concern. Location: pp. 11–13, especially the six-factor CFA comparisons on p. 13.

Under the usual unscaled maximum-likelihood definition with n = 296, RMSEA follows from χ²/df as the square root of (χ²/df − 1)/295, when the expression is positive. The six-factor model’s ratio of 2.58 implies approximately .073, rather than .06. The one-factor model’s ratio of 18.67 implies approximately .245, rather than .19. The intermediate comparisons also do not follow the same ordinary formula. Robust or scaled test statistics and robust RMSEA can differ, so this is a request to reconcile the estimator and correction, not a claim that every alternative formula is impossible.

The paper reports ratios without the actual χ² and degrees of freedom for most models. It also includes the two archival, single-indicator count outcomes as factors in a six-factor CFA after describing them as observed outcomes in the analysis rationale. Single-indicator factors can be specified, but their loadings, residual variances, identification constraints, treatment of counts, and role in factor-merging comparisons must be shown. Without that information, the claimed discriminant-validity evidence cannot be reconstructed.

F12: Additional descriptive and text-to-table discrepancies need correction

Major to minor, depending on the item. Location p. 11, 13, 20–21; Tables 2, 5, and 6; Appendix C; reference list p. 31.

The response rate in Study 1 is reported as 39%, but 346 responses from 914 invited eligible firms equal 37.86%, conventionally 38%. The final linked sample is 296/914 = 32.39%. If a different contact denominator was used, it should be stated. On p. 20, the explained variances are described as 23% for CLT, 27% for exploration, and 29% for exploitation. Table 6 Models 2, 4, and 8 instead give 25%, 29%, and 27%. On p. 21, Models 4 and 8 are said to include the mediator; Table 6 places CLT in Models 5 and 9.

The AVE references on pp. 13 and 20 point to Tables 2 and 4, respectively, although those tables do not contain the claimed AVE statistics. Appendix C points to Table 2 Model 2 for a regression that appears in Table 3, and to Table 3 for indirect effects presented in Table 4. These are localized citation errors, but they obstruct verification of already conflicting results. Reporting p = .000 should be replaced by an inequality reflecting the software’s precision. Kang and Snell (2009) is listed as Journal of Management Studies 45(1), whereas the publisher record gives 46(1), 65–92.

There is also a conditional descriptive inconsistency in the public/private variable. If it uses the apparent 1/2 coding, its reported means imply sample SD ranges of approximately .353–.363 in Study 1 and .331–.342 in Study 2, after allowing mean rounding. The tables instead report .38 and .35. This should be checked against the actual coding and frequency counts; the coding is not sufficiently documented to treat the calculation as unconditional.

Design and Causal Interpretation

F13: IC and CLT are measured simultaneously

Major; causal identification concern. Location: p. 11 and 18–19; Appendix C; Appendix D.

In both studies, the same CEO rates IC and CLT at T1. The later innovation measurement creates temporal separation between those variables and some outcomes, but does not establish that IC precedes CLT or that IC changes CLT. Stable organizational differences, prior innovation, management quality, learning history, and other common causes could generate their contemporaneous association. The reverse-path exercise in Appendix C does not resolve this problem.

The appropriate interpretation is a lagged-outcome association with a contemporaneous proposed mediator, subject to confounding and measurement assumptions. It is not a fully observed longitudinal mediation sequence. Maxwell and Cole (2007) and Maxwell, Cole, and Mitchell (2011) explain why longitudinal mediation parameters cannot generally be recovered from contemporaneous paths merely by attaching a later outcome. Future identification would require a design appropriate to the causal claim, such as repeated measurements of the relevant constructs with justified lags and confounder treatment, or credible experimental or quasi-experimental variation. A third wave by itself would not eliminate confounding.

F14: Study 2’s outcome window overlaps the purported baseline

Major; temporal interpretation concern. Location: p. 18–19 and 28; note 2 on p. 29; Appendix D.

Study 2 separates T1 and T2 by approximately nine months, but its R&D respondents assess innovation activities over the past year at T2. Approximately three months of that retrospective outcome window therefore precede T1. The outcome is not entirely subsequent to the measured IC and CLT. Describing the design simply as an examination of subsequent innovation overstates the temporal ordering.

Both studies also measure knowledge breadth and depth between T1 and T2, without sufficiently precise dates. Those moderators may partly reflect knowledge acquired during the same innovation interval that supplies the outcome. The issue is not that intermediate measurement is always invalid; it is that their treatment as preexisting conditions require justification. Report the measurement calendar, reference windows, and alignment for each variable. The claim that the shorter lag is necessarily a conservative test is also unsupported without a model of effect timing. A shorter lag can change bias, overlap, and the estimand in several directions.

F15: Prior innovation controls do not ensure that the models estimate change

Major; estimand and endogeneity concern. Location: p. 12, control variables; p. 19, control variables; note 3 on p. 29.

The article states that controlling prior innovation ensures that the analyses capture changes from T1 to T2. An outcome regression adjusted for a baseline measure estimates an association conditional on that measure; it does not automatically become a change model or a causal effect. Its interpretation depends on baseline reliability, the observation windows, the causal role of the controls, and unmeasured common causes. The lagged-count observation period in Study 1 needs specification.

Study 2 uses a five-item prior innovation performance scale in place of the two specific innovation outcome measures. A general performance control is not the same baseline construct as either exploration or exploitation. Its items and exact temporal reference are not supplied in Appendix A. The stronger change claim is therefore particularly difficult to sustain. The remedy is to define the estimand, disclose baseline measurement and timing, justify each control’s causal role, and use language that matches what the adjusted model estimates.

F16: Sampling and missingness limit the replication and population claims

Major; reporting and generalizability concern. Location: p. 10–11 and 18–19.

Study 1 narrows a frame of 1,491 firms to 914 with in-house innovation departments. It receives 346 responses, excludes 28 incomplete responses, and retains 296 after linking CEO, R&D, and archival records. Thus another 22 firms are lost after the initial completeness screen. Restricting the population to firms with an innovation department is defensible, but it makes the results conditional on an innovation-active organizational subset. Claims about firms generally should reflect that restriction.

The registry-based comparison of respondents and nonrespondents is a useful strength. However, nonsignificant differences in age, size, and organizational type do not establish the absence of selection on learning, innovation, or unobserved characteristics. Test statistics, effect sizes, group counts, and the separate reasons for each loss are needed. In Study 2, all 262 firms agreeing to participate reportedly survive matching. That is possible and is not evidence of an error, but a complete contact and retention flow would make the process inspectable. The IT, chemical, and food samples also need composition details and an explanation of industry differences; the public/private control is not an industry control.

F17: Common method concerns remain within important paths

Major; inference concern. Location p. 13 and p. 20; Appendix D.

Archival outcomes and multiple informants reduce some common method risks, but IC and CLT still share the CEO respondent and occasion. In Study 2, knowledge breadth, knowledge depth, and innovation are supplied by R&D managers, albeit at different points. These source overlaps are especially relevant to the mediation’s first stage and the second study’s conditional relationships.

Harman’s first-factor percentage does not establish the absence of common method bias. Nor does saying that an unmeasured method factor failed to improve fit provide an auditable result without the model, constraints, fit changes, and effect estimates. The claim that specifying IC as a higher-order construct reduces respondents’ tendency to perceive overlap confuses the analyst’s measurement model with the questionnaire experience. Questionnaire wording and arrangement may help; the later statistical representation is not itself a respondent-level intervention. The appropriate conclusion is that some risks were reduced and important residual risks remain. The methodological review by Podsakoff and colleagues (2024) supports treating method bias as more complex than a single-factor diagnostic.

Construct Definitions and Operationalization

F18: The CLT items do not directly measure the proposed transformation process

Major; construct validity concern. Location theory p. 5–6; measurement p. 11; discussion p. 26–28; Appendix A.

All seven CLT items ask about the extent of knowledge or technology transfer to the organization across functional domains. They do not directly assess whether recipients assimilate knowledge, challenge assumptions, recombine it, change routines, stabilize interpretations, or deliberately direct it toward exploration or exploitation. The amount of incoming transfer can also depend on opportunities, external partners, investment, or need, rather than solely on the firm’s capacity to learn and transform.

The authors explicitly acknowledge on p. 11 that this is a proxy. That acknowledgment is appropriate, but subsequent claims repeatedly treat the full theorized transformation mechanism as demonstrated. Broad coverage across functional destinations is not direct measurement of successful integration between functions. The instrument also asks questions about extent, whereas the measurement description says respondents indicated agreement with statements. The actual anchors and any adaptation must be disclosed.

The findings could, after numerical repair, support associations involving reported knowledge-transfer activity. Stronger claims about enacted transformation routines require direct content validation and measures of those routines or a clear narrowing of the construct label and conclusions. A favorable factor structure cannot establish the missing substantive content.

F19: The intellectual-capital measurement model changes without sufficient explanation

Major; construct specification and comparability concern. Location p. 11, 13, and 20; Appendix A.

Study 1 supports a three-factor IC structure and then uses IC as a single predictor, but does not adequately describe how the fourteen indicators or three dimensions become that score. Study 2 describes a reflective–formative higher-order construct. The paragraph on validity simultaneously refers to first- and second-order formative constructs, although the stated first-order dimensions are reflective. The three second-order coefficients are labeled λ, without clearly distinguishing formative weights from loadings.

These choices matter. A composite formed from distinct resource dimensions has a different meaning from a reflective common factor or an unweighted item average. The paper should justify whether its dimensions define IC or reflect an underlying common cause, report the exact scoring and higher-order estimation procedure, and provide weights, uncertainty, indicator relevance, and collinearity results as appropriate. Reporting only that VIFs are below ten is insufficient to inspect the actual values. Until these choices are clear, the two studies cannot be assumed to estimate precisely the same IC relationship.

F20: IC and the knowledge base need stronger substantive separation

Major; content validity and boundary-condition concern. Location p. 7–9 and 26–27; Appendix A.

The proposed distinction between IC as an infrastructure and knowledge breadth or depth as its content is conceptually possible. The operationalization makes the boundary less clear. Human-capital items already assess expertise, skill, and new knowledge; social-capital items assess sharing and applying knowledge across areas. Knowledge depth also assesses experience and technological knowledge. CLT then assesses knowledge transfer. Statistical separation of scales does not by itself explain where one resource or process ends and another begins.

The breadth scale combines customer diversity, market-segment knowledge, and R&D backgrounds; the depth scale combines customer experience, industry experience, and technological knowledge. Consequently, the discussion’s emphasis on market-facing knowledge is only one part of what the moderators measure. These are firm knowledge characteristics, not direct measures of an external environment favoring novelty or stability. A content map, discriminant validity evidence with full output, and more precise claims about internal knowledge configuration are needed. Report distributions as well, because restricted variation in these high-scoring scales can affect estimated interactions and their practical interpretation.

F21: The two studies operationalize innovation differently

Major; measurement and replication concern. Location p. 12 and 19; Appendix A; Appendix B.

Study 1 classifies product registrations or launches according to whether their technical category was already present in the firm’s T1 portfolio. This is a measure of category entry relative to the firm, not necessarily radical novelty to the market or the world. A product inside an existing category can still embody major technological novelty, and entry into a new category can involve imitation or licensing. The proxy is defensible, but the interpretation must match its level of novelty.

Appendix B improves transparency by specifying two independent coders, reconciliation, and use of company websites. It does not report pre-reconciliation agreement, the number of products, the ATC hierarchy level or device-category granularity, or evidence distinguishing registration dates from actual commercial launch dates. Its fixed T1 portfolio rule also means all later products in a previously absent category can be classified as exploratory; that rule should be explicit when interpreting the counts.

Study 2 measures reported activities. Its exploitative items concern efficiency, cost reduction, and automation in producing goods or services, while Study 1 counts products in established technical categories. Its exploratory items likewise capture orientations and activities rather than realized product output. The second study is therefore a conceptual extension with different measures, not a strict replication of identical innovation outcomes. The paper should explain the common conceptual target and the limits of cross-study comparisons.

Model Specification and Robustness

F22: The interaction models omit IC and do not isolate the reported incremental variance

Critical for reproducibility; major specification concern. Location Table 3 Models 7 and 12, p. 16; Table 6 Models 6 and 10, p. 23; p. 21.

The displayed interaction models include CLT, breadth, depth, their two product terms, and controls, but leave the IC row blank. In a second-stage moderated mediation outcome equation, the direct IC path ordinarily remains alongside the mediator and interaction terms. If the blanks indicate omission, the interaction equations do not represent the same conditional mediation model as the equations retaining IC. If IC was estimated but suppressed from the table, the table is incomplete. Either explanation requires correction and full equations.

The comparisons also change several terms at once. In Study 2, moving from Model 5 to Model 6 or from Model 9 to Model 10 removes the displayed IC term and introduces both knowledge main effects and interactions. The resulting R² changes do not isolate the contribution of interaction terms and are not simple nested additions to the preceding model. Table 6 shows increase of .03 and .04, while the text characterizes interaction gains as approximately 2%–3% and gives effect sizes of 2.7% and 2.5% without a reproducible mapping. The remedy is to retain the same sample and main effects, add interactions in an explicit nested step, define any f² statistic, and report the complete moderated mediation model.

F23: The evidence for differentiated moderation requires direct contrasts

Major; inferential concern. Location p. 15, 21, and 24–27; Figures 2–5.

A significant breadth interaction for exploration and a nonsignificant depth interaction for exploration do not by themselves show that the interactions differ from each other. The analogous point applies to exploitation and to comparisons across the two outcomes. The hypotheses about individual positive moderation can be evaluated with their own intervals, but the stronger conclusion that breadth and depth have empirically different or exclusive roles requires a direct contrast on a meaningful common scale.

Study 1 does report indices of moderated mediation, which is the appropriate type of quantity for testing whether a linear indirect effect varies with a moderator (Hayes, 2015). The numerical conflicts and model omissions elsewhere nevertheless prevent those reported indices from being reproduced. Study 2 needs an equally clear distinction between the path interaction, its indirect-effect index, and contrasts between moderator levels. Significance of an indirect effect at all three levels does not itself test whether those indirect effects differ.

Figures 2–5 illustrate predicted slopes but do not supply sufficient plotting coordinates, conditioning values, score transformations, or uncertainty to reconstruct them. Their visual appearance cannot independently validate moderated mediation. Provide equations, moderator values in original units, the values held fixed, and confidence intervals or the underlying prediction data.

F24: The count-model robustness check is too incomplete to verify the stated equivalence

Major; reproducibility and estimand concern. Location p. 15; Appendix E.

Appendix E reports means of 4.12 and 6.67, variances of 2.30 and 4.62, and dispersion statistics below one. These variance values agree with the rounded SDs in Table 2. Underdispersion is not a reason to declare a robust Poisson conditional-mean model automatically invalid, and the use of counts does not itself prove that the OLS analysis is wrong. The relevant questions concern the mean specification, uncertainty estimator, and target effect.

However, the appendix supplies only selected coefficients and an assertion that all specified conditional indirect-effect intervals exclude zero. It does not provide those indirect estimates or intervals, the full outcome equations, complete controls, model fit, or the mediation calculation. This falls short of p. 15’s promise of full diagnostics and model estimates. A Poisson coefficient is on a log-mean scale; its magnitude cannot be directly equated to an OLS coefficient in count units. State whether the mediation target is on the link scale or expected-count scale, report the complete calculation and bootstrap procedure, and compare effects in common, interpretable units. A nonsignificant Poisson-versus-negative-binomial test is also not a general validation of the conditional mean.

F25: The composite ambidexterity analysis does not establish masking

Major; interpretation and scaling concern. Location p. 24–25.

The additional analysis multiplies exploration and exploitation, and separately takes their absolute difference. The paper interprets nonsignificant moderation in these composite models as evidence that aggregation masks differentiated contingency effects. Changing the dependent variable changes the estimand, variance, reliability, and power. The disappearance of significance therefore does not identify masking as its cause.

The scales also matter. In Study 1, exploration and exploitation have different means and SDs, 4.12 and 1.52 versus 6.67 and 2.15. An absolute difference partly reflects those different levels and spreads; an uncentered product depends on the scales’ origins as well as their joint magnitude. These indices can be useful when theoretically justified, but their transformations and interpretation must be stated. Full models for both studies, uncertainty, and a direct comparison addressing the claimed information loss are needed. The reported γ = .21 and indirect effect .07 alone do not validate the broader masking claim.

F26: The estimator rationale and analytical record are insufficiently specified

Major; reporting and methodological rationale concern. Location p. 12–13 and 19–21; Tables 3–6.

Observed single-indicator outcomes do not preclude structural equation modeling. Conversely, hierarchical constructs and interactions do not by themselves establish that PLS yields more accurate estimates than covariance-based alternatives. The choice should follow the measurement ontology, target estimand, distribution, identification, and model assumptions. PROCESS and PLS can both be defensible, but the broad superiority claims do not justify these particular specifications.

Reproduction requires the PROCESS version and model syntax, every model equation, coefficient standardization conventions, score construction, missing-data handling, actual model-specific sample sizes, centering or scaling, interaction construction, standard-error options, bootstrap interval type and seed, and full output. For PLS, the higher-order estimation approach, weighting mode, interaction method, convergence settings, and actual Q² values and procedure are also necessary. The paper reports positive Q² and selected SRMR values without enough detail to reproduce those diagnostics. A claim of predictive relevance should be kept distinct from evidence of performance on genuinely held-out observations.

Theory, Contribution, and Claim Calibration

F27: The novelty claim should be narrowed against close antecedents

Major; contribution-framing concern. Location abstract p. 1–2; introduction p. 2–4; discussion p. 25–27.

The broad proposition that learning capabilities connect intellectual capital to innovation is established in closely related work. Hsu and Fang (2009) explicitly study organizational learning capability as a mediator between intellectual capital and new product development performance. Farzaneh and colleagues (2022) report an indirect relationship between intellectual capital and innovation ambidexterity through dynamic capabilities, conditioned by innovation orientation. Zhou and Li (2012) examine interactions between knowledge breadth or depth and knowledge integration mechanisms in explaining radical innovation.

These antecedents do not make the present paper devoid of potential contribution. Distinguishing exploration and exploitation and testing specific conditional indirect relationships could add value. The contribution must identify the precise new mechanism, boundary condition, or empirical distinction beyond those antecedents. Renaming a learning or transfer construct, or reproducing the general resource–capability–innovation sequence, is insufficient on its own. The paper should narrow its claims to the element that is theoretically differentiated and actually measured, after its numerical evidence is repaired.

F28: The contrast with absorptive capacity is overstated

Major; conceptual distinction concern. Location p. 5 and p. 26; note 1 on p. 29.

The article initially defines absorptive capacity to include commercial application, then characterizes it primarily as acquisition and assimilation while assigning transformation and organizational use to CLT. That contrast neglects the established transformation and exploitation dimensions of absorptive capacity, notably the potential/realized distinction in Zahra and George (2002). It therefore does not, as stated, establish that CLT occupies a distinct conceptual space.

The discussion then describes CLT as a capability for acquiring and transforming external knowledge, further weakening the proposed separation. Wang, Chen, and Lawler’s (2022) source study also locates CLT in learning and transforming external knowledge and technologies. The appropriate correction is a systematic comparison of construct content, process stages, and measurement, followed by a narrower distinction if one remains. A different label or a favorable CFA comparison among the present scales does not resolve overlap with an adjacent construct that was not measured.

F29: Two integration logics and necessity are theorized but not tested

Major; mechanism and logical overreach. Location p. 5–6 and 25–27; Figure 1, p. 4.

The theory says that CLT is not a single undifferentiated mediator and proposes exploratory and exploitative integration logics. Empirically, the model uses one general CLT measure and two outcomes. Neither integration logic is separately measured, and no managerial deployment decision, routine adaptation, or process sequence is observed. Different associations with two outcomes do not demonstrate that the proposed internal logics produced them.

Helfat and Winter (2011) do discuss the blurred boundary between dynamic and operational capabilities and the possibility of dual-purpose capabilities. Thus, the idea that a capability can serve different purposes is not inherently unsupported. The problem is the empirical claim that these specific purposes and their operation have been established here. Likewise, positive mediation does not prove that intellectual capital cannot yield innovation without CLT. The reported direct IC paths remain positive after introducing CLT. Necessity language should be replaced by a qualified account of a proposed contributing pathway unless necessity is separately theorized and tested.

F30: Corporate entrepreneurship, context, success, and managerial prescriptions exceed the measured evidence

Major; scope and practical-inference concern. Location abstract p. 1–2; p. 26–28.

The studies measure aspects of innovation and knowledge, not the full domain of corporate entrepreneurship, strategic renewal, or venturing. The Iranian setting supplies contextual relevance, but institutional turbulence is neither measured as a varying explanatory condition nor compared with a less turbulent setting. The data therefore do not establish that turbulence amplifies the mechanism. Similarly, product-category counts and innovation activities do not measure commercial success, profitability, customer validation, or resilience, although the discussion sometimes moves to those outcomes.

The managerial recommendations propose deliberate steering of CLT, selective investments because breadth and depth are costly to develop together, and risks from applying specialist routines to exploratory initiatives. The studies do not measure those costs, investment tradeoffs, steering decisions, or harmful misallocation. In particular, a nonsignificant cross-interaction does not demonstrate that the corresponding knowledge investment damages innovation. These ideas can be offered as theoretically motivated possibilities, but should not be presented as demonstrated managerial consequences. The conclusion should distinguish observed associations, proposed mechanisms, and untested prescriptions.

Implications for the Hypotheses

The proper present verdict is that the hypotheses are not reproducibly established by the published results. That differs from concluding that the hypotheses have been disproved. Positive reported estimates and intervals may ultimately survive correction, but their values and specifications must first be reconciled.

Table R6: Current evidential status

Claim	Published interpretation	Assessment after audit
H1a and H1b	CLT mediates IC effects on both innovation outcomes.	Reported support is not reproducible from the conflicting coefficients, R² values, and indirect effects. Causal mediation is additionally unidentified.
H2a	Breadth strengthens the indirect path to exploration.	The claimed pattern requires corrected full models, consistent indirect-effect arithmetic, and an auditable moderation index.
H2b	Depth strengthens the indirect path to exploitation.	The same reproducibility limitations apply, including the incorrect mean-to-high contrast in Study 2.
Differentiated roles	Breadth and depth play distinct contingent roles.	Individual significance patterns do not establish differences between coefficients; direct contrasts are needed.
Mechanism and practical effects	CLT transforms resources through specific routines and improves managerial outcomes.	Transfer items and observational associations do not directly test those routines, necessity, investment tradeoffs, or commercial success.

Required Reconciliation and Editorial Response

The numerical conflicts warrant a formal request to the authors and journal for a documented reconciliation. Correcting isolated typographical errors would be sufficient only if independently checked output shows that the underlying analyses are coherent and that the corrected conclusions follow. Because the discrepancies span correlations, fit, coefficients, indirect effects, and two studies, the response should examine the full analytical record rather than patch individual cells in isolation.

Table R7: Materials and corrections needed to resolve the findings

Priority	Required material or action	Purpose
1	Original, unedited output for both studies, with model labels, dates, and table-generation records	Resolve contradictory values and the repeated control sequences.
1	Analysis-ready deidentified data or controlled independent access; variable dictionary and complete scoring code	Reproduce correlations, distributions, sample sizes, and regressions without compromising respondents.
1	Full PROCESS syntax, PLS project, and SEM syntax, including the alternative reverse models	Identify omitted IC terms, scale conventions, model changes, and the basis of the reverse-direction claims.
1	Original bootstrap estimates, interval definitions, seeds, and conditional-effect output	Reconcile path products, moderator contrasts, ω, Δ, and the reported confidence intervals.
2	Complete measurement output, standardized loadings, residuals, weights, reliability definitions, AVE and HTMT tables	Resolve measurement-statistic discrepancies and clarify the higher-order IC construct.
2	Respondent flow, missingness and matching log, exact dates, and reference windows	Assess selection and the temporal ordering of each proposed pathway.
2	Product-level coding protocol, category hierarchy, dates, coder agreement, and reconciliation log	Validate the archival innovation proxies and clarify registrations versus launches.
2	Full count, interaction, composite-outcome, and plotting specifications and outputs	Make the claimed robustness and graphical results independently inspectable.
3	Revised theory, abstracts, discussion, and limitations linked to corrected evidence	Remove unsupported causal, novelty, necessity, success, and managerial claims.

An independent analyst should first reproduce all tables from the same analysis-ready datasets and scripts, then establish a single internally coherent version of each study. The next step is to rerun the specified mediation and moderation analyses with complete controls and clearly defined scales. Construct and causal claims should then be revised to match the design. If original output cannot reconcile the published results, the journal would have grounds to consider a more substantial corrective action under its procedures. The present review does not prescribe retraction or assign intent without that investigation.

References

Farzaneh, M., Wilden, R., Afshari, L., and Mehralian, G. (2022). Dynamic capabilities and innovation ambidexterity: The roles of intellectual capital and innovation orientation. Journal of Business Research, 148, 47–59. https://doi.org/10.1016/j.jbusres.2022.04.030

Hayes, A. F. (2015). An index and test of linear moderated mediation. Multivariate Behavioral Research, 50(1), 1–22. https://doi.org/10.1080/00273171.2014.962683

Helfat, C. E., and Winter, S. G. (2011). Untangling dynamic and operational capabilities: Strategy for the (n)ever-changing world. Strategic Management Journal, 32(11), 1243–1250. https://doi.org/10.1002/smj.955

Hsu, Y.-H., and Fang, W. (2009). Intellectual capital and new product development performance: The mediating role of organizational learning capability. Technological Forecasting and Social Change, 76(5), 664–677. https://doi.org/10.1016/j.techfore.2008.03.012

Kang, S.-C., and Snell, S. A. (2009). Intellectual capital architectures and ambidextrous learning: A framework for human resource management. Journal of Management Studies, 46(1), 65–92. https://doi.org/10.1111/j.1467-6486.2008.00776.x

Maxwell, S. E., and Cole, D. A. (2007). Bias in cross-sectional analyses of longitudinal mediation. Psychological Methods, 12(1), 23–44. https://doi.org/10.1037/1082-989X.12.1.23

Maxwell, S. E., Cole, D. A., and Mitchell, M. A. (2011). Bias in cross-sectional analyses of longitudinal mediation: Partial and complete mediation under an autoregressive model. Multivariate Behavioral Research, 46(5), 816–841. https://doi.org/10.1080/00273171.2011.606716

Podsakoff, P. M., Podsakoff, N. P., Williams, L. J., Huang, C., and Yang, J. (2024). Common method bias: It’s bad, it’s complex, it’s widespread, and it’s not easy to fix. Annual Review of Organizational Psychology and Organizational Behavior, 11, 17–61. https://doi.org/10.1146/annurev-orgpsych-110721-040030

Wang, P., Chen, X., and Lawler, J. J. (2022). Unraveling the relationship between high-performance work systems and firm performance: A mediation analysis. Human Resource Management, 61(2), 181–197. https://doi.org/10.1002/hrm.22087

Zahra, S. A., and George, G. (2002). Absorptive capacity: A review, reconceptualization, and extension. Academy of Management Review, 27(2), 185–203. https://doi.org/10.5465/amr.2002.6587995

Zhou, K. Z., and Li, C. B. (2012). How knowledge affects radical innovation: Knowledge base, market knowledge acquisition, and internal knowledge sharing. Strategic Management Journal, 33(9), 1090–1102. https://doi.org/10.1002/smj.1959

Don’t forget to leave a comment if you find this article interesting.

About the Author: This investigation was conducted by an anonymous professor at a renowned university.

Click to Read Previous Article